The Use of the Prevena™ Incision Management System on Post-Surgical Cesarean Section Incisions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Use of the Prevena™ Incision Management System on Post-Surgical Cesarean Section Incisions (NCT01450631), a randomized na study. The primary outcome is Incidence of Postoperative Surgical Site Occurrences (SSOs) up to Day 42 (+/- 10 Days) Post Cesarean Section Surgery..

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group evaluation of an incision-management device and a standard dressing in obese subjects undergoing Cesarean section surgery. The registry lists the study as completed, with enrollment of 92. Its start is recorded as 2012-02 and primary completion as 2013-12. The phase is listed as NA. The sponsor was KCI USA, Inc.

Participants were assigned to Prevena™ (PIMS) or standard dressing. The registry describes no masking. The standard-dressing arm used sterile gauze and a non-penetrable barrier over the sutured incision. The PIMS arm used a disposable, battery-powered unit intended to apply continuous -125 mmHg negative pressure over a 7-day therapy period. The record does not describe allocation concealment, the randomization sequence, or whether any procedures were used to limit differences in care beyond the assigned dressing.

The primary endpoint was assessed through Post-op Day 42 (+/- 10 days). Its analysis population was per protocol, as were the primary and secondary endpoint analyses generally described in the registry. The posted primary endpoint counts include 43 participants in the standard-dressing group and 39 in the PIMS group. These arm counts are not the same as the enrollment figure. Reasons for the difference, including exclusions or missing outcome assessments, are not reported in the registry record.

The registry identifies one secondary outcome: surgical incision intervention through Day 42 (+/- 10 days). The study therefore provides information on a defined postoperative period and a specific surgical setting, rather than on other procedures or longer-term outcomes. Details of the original sample-size justification, planned analysis methods, and any interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Per-protocol Population was used for primary and secondary endpoint analysis.

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 Incidence of Postoperative Surgical Site Occurrences (SSOs) up to Day 42 (+/- 10 Days) Post Cesarean Section Surgery., measured over Post-op Day 42 (+/- 10 days) after Cesarean section surgery.

The primary endpoint is the incidence of postoperative surgical site occurrences (SSOs) through Post-op Day 42 (+/- 10 days) after Cesarean section surgery. It is reported as the number of participants with an event, rather than as a continuous measurement. The registry includes several kinds of wound-related findings within this endpoint: an unanticipated local inflammatory response, prolonged drainage, fluid collection, dehiscence, and surgical site infection.

A composite endpoint groups multiple clinically relevant event types into one outcome. In general, this can capture a broader range of postoperative problems than any single component would capture alone. It can also make interpretation less specific: a group-level difference in the composite does not reveal, by itself, which component contributed most. The registry does not report separate primary results for each listed SSO component, so their individual patterns cannot be assessed from the posted primary outcome.

The endpoint is used to compare how often participants in the two assigned groups had at least one recorded SSO within the specified follow-up period. It is a binary outcome at the participant level: a participant either contributes to the event count or does not. The registry states that the per-protocol population was used for primary and secondary endpoint analysis. It does not describe the operational rules for adjudicating events, the source of outcome assessments, or how incomplete follow-up was handled. Those details are important for understanding exactly how the endpoint was captured and are not reported in the registry record.

7. Results Posted in the Registry

• Prevena™ (PIMS): 5.1% (2/39) versus 16.3% (7/43) on control; risk difference -11.2 percentage points (95% CI -24.2 to 1.9), risk ratio 0.32 (0.07–1.43); unadjusted two-proportion z-test p = 0.107.

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.

Incidence Rate of Surgical Incision Intervention (SII) up to Day 42 (+/- 10 Days) Post Cesarean Section Surgery.

• 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:
  • Prevena™ (PIMS): 2.6% (1/39) versus 14.0% (6/43) on control; risk difference -11.4 percentage points (95% CI -22.9 to 0.1), risk ratio 0.18 (0.02–1.46); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Prevena™ (PIMS) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoint concerns surgical incision intervention through Day 42 (+/- 10 days), a related postoperative outcome but not the same measure as the primary composite of SSOs. The posted group pattern is directionally consistent with the primary comparison: fewer participants in the PIMS group had the recorded secondary outcome than in the standard-dressing group. The secondary comparison remains uncertain, and its confidence interval reaches across the no-difference reference value. It therefore does not resolve the uncertainty in the primary result.

Related endpoints can contribute context because they assess different aspects of postoperative care. Agreement in direction may make the overall pattern easier to describe, but it does not transform either estimate into conclusive evidence. The secondary endpoint is not a replacement for the prespecified primary endpoint, and the registry does not report a combined analysis that joins the two outcomes. Nor does it post results for additional secondary endpoint analyses beyond the listed outcome.

Unadjusted secondary results generally carry less weight when several outcomes or comparisons are examined. In general, testing multiple outcomes increases the chance that at least one result will appear notable through random variation alone. Adjustments or a prespecified hierarchy can address that concern, but the registry does not report a multiplicity procedure or a detailed hierarchy for the outcomes. It lists no reported analyses for the secondary endpoint. The posted unadjusted comparison should therefore be treated as supportive descriptive information rather than as independent confirmation of the primary finding.

The secondary result also depends on the same broad design and reporting limitations: the endpoint analysis is per protocol, and the record does not explain exclusions, missing outcome data, event ascertainment, or the statistical method. Those omissions make it difficult to judge how robust the secondary pattern is to analysis choices. The appropriate overall reading is that the secondary endpoint points in the same direction as the primary comparison, while adding limited evidence about whether a true difference exists or how large it might be.

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

• Incidence Rate of Surgical Incision Intervention (SII) up to Day 42 (+/- 10 Days) Post Cesarean Section Surgery.

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, each participant is classified according to whether the event was recorded during the specified follow-up period. The primary outcome is reported as counts of participants with SSOs in each arm. In general, comparing such groups involves estimating the event risk within each group and then expressing the contrast on a chosen scale. The reported primary contrast is a risk difference for PIMS relative to standard dressing. A negative risk difference indicates that the observed event risk was lower in the PIMS group; it does not, on its own, establish a causal effect or statistical certainty.

What does the risk difference describe?

The risk difference compares the proportion with an event in one group with the proportion in the other. It is an absolute contrast, expressed as a difference in risks rather than a relative multiplier. The registry reports the risk difference as -0.112. The confidence interval runs from -0.242 to 0.019. Because the interval includes zero, the posted uncertainty range includes no difference as well as differences in either direction. No recalculation is needed to interpret that feature: zero is the no-difference value on the risk-difference scale.

The registry also posts relative measures, including a risk ratio of 0.315 with a confidence interval from 0.070 to 1.427, and an odds ratio of 0.278 with a confidence interval from 0.054 to 1.429. These measures use different scales from the risk difference. A risk ratio compares risks as a ratio; an odds ratio compares odds. In general, relative measures can look more or less dramatic than absolute contrasts, especially when the outcome is uncommon. Their confidence intervals are wide and include the no-association value of 1, so they also reflect considerable uncertainty. The registry's listed unadjusted p-value for the primary comparison is 0.107.

What does a confidence interval contribute?

In general, a confidence interval conveys the range of estimates compatible with the observed data under the specified statistical procedure and its assumptions. It is not a guarantee that the true effect lies inside the interval, and it is not a range containing a fixed probability for this particular trial's effect. Its width is informative: a wider interval means less precision. For a risk difference, zero represents no group difference. For a ratio measure, 1 represents no group difference. The primary intervals cross those respective reference values, so the data do not sharply distinguish a difference from no difference.

A p-value addresses a related but different question. In general, it describes how unusual the observed data, or data more extreme, would be if a specified null hypothesis and analysis model were true. It does not measure the size or clinical importance of an effect. Nor is it the probability that the null hypothesis is true. A p-value should be read with the estimate, interval, endpoint definition, and analysis population, rather than treated as a stand-alone verdict.

Why does the analysis population matter?

The registry states that the per-protocol population was used for primary and secondary endpoint analysis. In general, a per-protocol analysis focuses on participants who met the protocol-defined requirements for analysis, but the exact definition varies by study. The registry does not report those requirements, the number excluded from each analysis, or the reasons for exclusion. Randomization supports balanced comparison at assignment; exclusions after assignment can make the analyzed groups less directly comparable. The record does not provide enough detail to evaluate whether that occurred.

The primary outcome is a composite, and the registry gives a single participant count for the combined SSO definition. In general, combining components can provide a broad measure of event occurrence, while concealing differences among event types. The record does not report separate statistical tests for the individual components. It also does not report the statistical model, any covariate adjustment, or the method used to construct the intervals and p-value. The reported values can be interpreted on their stated scales, but the absent analysis details limit a fuller assessment of the calculation choices.

What can planning calculations tell readers?

The registry includes planning illustrations based on fractions of the observed effect. In general, these calculations translate an assumed effect size and statistical design into a sample-size requirement under stated assumptions. They are not a substitute for a trial's original design rationale. The original sample-size justification and its assumptions are not reported in the registry record. The listed planning assumptions and the meaning of the per-arm figures are described separately in the sample-size reading.

For binary outcomes, a useful statistical concern is sparse event information. When event counts are small, estimates can be unstable and confidence intervals can be broad. This is a general principle, not a claim that a particular model was used in this trial. Over-dispersion is a concern mainly for count data when variability exceeds what a simple probability model expects; it is not the central issue for this participant-level binary endpoint. The registry does not report a model-based analysis addressing over-dispersion or other departures from assumptions.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.112, and its 95% confidence interval extends from -0.242 to 0.019. That interval is wide enough to include estimates on both sides of zero. In practical statistical terms, the data are compatible with a meaningful difference in the direction of fewer SSOs with PIMS, with little or no difference, and with a small difference in the opposite direction. The point estimate alone should not be treated as the settled effect.

The relative measures tell a similar precision story. The risk ratio is 0.315, with a 95% confidence interval from 0.070 to 1.427. The odds ratio is 0.278, with a 95% confidence interval from 0.054 to 1.429. Both intervals include 1, the no-association value for a ratio, and each covers a broad range. The distinct scales do not remove the underlying uncertainty in the event data.

In general, confidence-interval width reflects both the amount of information in the data and the variability of the outcome, as well as the analysis method. A small number of events can produce imprecise estimates even in a randomized trial. The primary analysis includes 7 events in the standard-dressing group and 2 in the PIMS group. The registry does not report interval construction details, so the precision can be described from the posted limits, but the assumptions behind those limits cannot be independently evaluated from the record.

The interval is more informative than a binary declaration of statistical significance because it shows the range of uncertainty and the directions still compatible with the data. It does not establish that every value in the interval is equally plausible, nor does it express clinical importance. The registry does not state a threshold for a difference that would be considered important. Thus, precision and practical importance are separate questions, and the latter cannot be resolved from the numerical comparison alone.

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 events. That format applies to these binary outcomes; the registry's general note distinguishes time-to-event calculations, which would give total events, but the posted outcomes are participant event counts. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the assumed effect under those assumptions, if that effect were the true effect. The 90% column gives the corresponding planning estimate for a higher chance of detection. These are design calculations, not a guarantee that a future study will produce a particular result. Smaller effects require more participants to distinguish them from random variation, which is why the planning requirements rise as the assumed fraction of the observed effect becomes smaller.

The registry does not report the trial's own original sample-size justification, so these calculations should not be read as the enrollment target used to design this study. They are illustrations computed from the observed effect and stated assumptions, not observed power. The original assumptions for the trial's design are not reported in the registry record. They also do not indicate whether any specific future study would be adequate, since that depends on its target effect, outcome frequency, design, and analysis choices.

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 = 0.163; treatment proportion p₁ = 0.051; average p̄ = 0.107.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4372 = 0.8569.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4300 = 0.3619.
4. n = (0.8569 + 0.3619)² / (-0.1115)² = 119.5, rounded up to 120 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 <- 0.162790697674419                          # control proportion
p1 <- 0.0512820512820513                          # 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(1450631)
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 = 120 (80% power), 160 (90% power)
 75% of observed effect: n per arm = 238 (80% power), 318 (90% power)
 50% of observed effect: n per arm = 589 (80% power), 787 (90% power)
power.prop.test: 119.5 
Simulated power at n = 120 per arm: 0.823 (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 evaluates more than one outcome, contrast, subgroup, or analysis. In general, the more statistical tests conducted, the greater the chance that at least one will appear unusual by chance if all underlying null hypotheses are true. One way to address this is to define a primary endpoint and a testing hierarchy in advance; another is to adjust the interpretation or error rate for multiple tests. The registry identifies a primary endpoint and one secondary outcome, but a multiplicity strategy is not reported in the registry record.

The registry reports no analyses for the secondary endpoint, despite posting its outcome counts and comparison. The reason is not reported in the registry record. It is also not clear from the record whether other analyses were planned, whether subgroup or sensitivity analyses were conducted, or whether any results were omitted. These omissions limit the ability to assess how the reported comparisons fit into the full set of analyses that may have been considered.

Missing-data handling is also not described. The registry does not report how many participants lacked an endpoint assessment, whether missing outcomes were imputed, or what assumptions would have been used for incomplete follow-up. The primary endpoint counts are reported for 43 participants in the standard-dressing group and 39 in the PIMS group, while overall enrollment is 92. The record does not explain the difference between enrollment and the endpoint analysis counts, so the reasons should not be inferred.

The analysis population is described as per protocol, but its operational definition, the exclusions applied, and the number excluded for each reason are not reported in the registry record. The record also does not report an intention-to-treat analysis or a comparison of results across analysis populations. In a randomized trial, the assigned groups are formed by randomization; restricting analysis after assignment can affect comparability if the reasons for exclusion are related to outcomes or treatment. The available information is not enough to determine whether this concern applies.

Other important statistical-plan details are unreported: the trial's original sample-size justification, the planned model and covariate adjustments, interim analyses, stopping rules, and methods for handling multiple endpoints. Their absence does not show that these procedures were not used; it means the registry record does not document them. That distinction matters when evaluating the completeness and reproducibility of the posted statistical results.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiomyopathy (2.2%), gastric ulcer perforation (2.2%), endometritis (2.2%), pneumonia (2.2%), seroma (2.2%).

The registry lists adverse-event risk sets of 46 in each group. The recorded serious adverse-event affected counts are 2 for standard dressing and 4 for PIMS. The other adverse-event affected counts are 9 and 12, respectively. These are descriptive counts, and the registry record does not provide a comparative statistical analysis of these safety figures. The safety risk sets differ from the primary endpoint analysis counts; the reason for that difference is not reported in the registry record.

The record lists Cardiomyopathy, Gastric Ulcer Perforation, Endometritis, Pneumonia, and Seroma among the top serious terms, each at 2.2%. The information posted does not establish that these terms were caused by either dressing, nor does it give enough detail to assess timing, severity beyond the serious classification, or relatedness. Deaths are not reported in the registry record.

In general, adverse-event counts are most informative when read alongside definitions, exposure time, ascertainment procedures, and attribution methods. Those details are not reported in the registry record. The counts should therefore be read as the safety information recorded for the groups, not as a causal comparison or a comprehensive account of risk.

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

The results describe a randomized comparison of PIMS and standard dressing among obese subjects undergoing Cesarean section, with outcomes assessed through Day 42 (+/- 10 days). The primary endpoint counts were lower in the PIMS group, and the point estimate of the risk difference was in that direction. The confidence interval, however, includes no difference and values on either side of it. The posted primary comparison is therefore uncertain rather than definitive.

These findings do not establish that PIMS prevents postoperative occurrences, that standard dressing is better, or that the two approaches are equivalent. A non-significant or uncertain result is not proof that no effect exists. Conversely, a difference in observed counts is not proof of a treatment effect. The study's estimate needs to be interpreted with its uncertainty interval, per-protocol analysis population, composite endpoint, and incomplete reporting of methods and missing data.

The endpoint combines several types of postoperative wound occurrence, and the record does not show how the individual components contributed. The findings are tied to the registry's specified population and surgical setting. They should not be generalized automatically to other procedures, populations, care settings, or follow-up durations. The record reports a secondary incision-intervention outcome with a broadly consistent direction, but its unadjusted status and the absence of a reported multiplicity plan give it limited confirmatory weight.

The adverse-event information is also descriptive. It supplies group counts and several listed serious terms, but not the methods needed to determine attribution or a comparative safety effect. Overall, the registry gives a useful account of the outcomes and estimates it posts, while leaving important questions about precision, analysis populations, missing data, and statistical planning unresolved. The results characterize the evidence available in this record; they do not offer medical advice or a conclusion about treatment choice.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a directional point estimate and a precise, conclusive comparison. The primary estimate favors fewer recorded SSOs in the PIMS group on the risk-difference scale, while the confidence interval remains compatible with no difference and with effects in either direction. That distinction is central to sound interpretation: the observed direction is not the same as certainty about the underlying effect.

The outcome is a composite, which broadens the scope of the primary measure but limits component-specific interpretation. The secondary endpoint is related and points in a similar direction, yet it does not remove uncertainty or serve as a confirmed replication. These features show why endpoint definitions and the hierarchy among outcomes matter alongside statistical estimates.

The record also highlights the importance of analysis populations and transparent reporting. The primary analysis is per protocol, but the record does not define the population in detail or explain the difference between enrollment and the reported arm counts. Missing-data procedures, multiplicity handling, and the original sample-size rationale are not reported in the registry record. Those omissions make it harder to assess how robust the estimates are and how the analyses were chosen.

Finally, the sample-size illustrations distinguish planning from inference. They are calculations based on observed effects and stated assumptions, not evidence of the trial's original design adequacy. Reading them alongside the uncertainty in the outcome estimates reinforces a broader statistical point: a small event count and a wide interval can leave an important question unresolved even when the observed group pattern is easy to describe.

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 limitations are specific to the available record. The endpoint analysis used the per-protocol population, but the registry does not define the criteria for that population, list exclusions, or explain why the endpoint counts differ from overall enrollment. The record does not say whether all randomized participants were included in a separate analysis or how missing assessments were handled. These gaps restrict evaluation of the effect of post-randomization exclusions and incomplete follow-up.

The primary outcome combines inflammatory response, prolonged drainage, fluid collection, dehiscence, and surgical site infection. The registry posts the composite count but not component-level results, making it impossible to see whether one type of event drove the overall pattern. It does not describe event adjudication, assessor procedures, or the statistical method used for the primary comparison. Masking is listed as none, but the record does not clarify which parties were unmasked or how outcome assessment was conducted.

The primary comparison has limited precision, reflected in a confidence interval that covers no difference and effects in either direction. The number of recorded events is small, so estimates and relative measures should be interpreted cautiously. The registry does not report baseline characteristics, detailed eligibility criteria, or information that would allow assessment of balance on prognostic factors in the analyzed population.

Other limitations concern reporting rather than demonstrated flaws: the original sample-size justification, interim analyses, multiplicity procedures, and detailed statistical analysis plan are not reported in the registry record. The single listed secondary outcome has no reported analyses, and the reason is not stated. The follow-up is bounded by the Day 42 (+/- 10 days) assessment window, so the record does not establish outcomes beyond that period.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Use of the Prevena™ Incision Management System on Post-Surgical Cesarean Section Incisions — NCT01450631.
• Registry record last updated 2024-10-16; status last verified 2024-10.
• Results first posted 2014-08-01.
• 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

The registry describes a completed, randomized, unmasked, parallel-group study of Prevena™ Incision Management System versus standard dressing in obese subjects undergoing Cesarean section surgery. Enrollment was 92. The primary outcome was postoperative surgical site occurrences through Post-op Day 42 (+/- 10 days), analyzed in the per-protocol population. The posted primary counts were 7 of 43 participants with standard dressing and 2 of 39 with PIMS.

The reported risk difference was -0.112, with a 95% confidence interval from -0.242 to 0.019 and an unadjusted p-value of 0.107. The interval includes no difference and reflects substantial uncertainty. One secondary outcome, surgical incision intervention through Day 42 (+/- 10 days), is listed. Adverse-event counts are reported descriptively. Important details about missing data, analysis methods, multiplicity, and the original sample-size rationale are not reported in the registry record.