Subcuticular Absorbable Staples Versus Conventional Skin Closure in Women Undergoing Cesarean Delivery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Subcuticular Absorbable Staples Versus Conventional Skin Closure in Women Undergoing Cesarean Delivery (NCT05112640), a randomized na study. The primary outcome is Operating Time.

2. Clinical Question

The clinical question is whether closing a cesarean skin incision with an absorbable subcuticular stapling device is associated with a different operating time than closing it with conventional subcuticular Monocryl suture. The registry also describes wound cosmetics as an objective and posts selected secondary results on wound appearance, wound complications, and postoperative pain.

The registry describes the broader objective as assessing both operative time and wound cosmetics. Those questions are related but not interchangeable: operating time measures elapsed time across the specified portion of the procedure, while wound cosmesis concerns a separate score assessed from surgery through six weeks post partum. The posted primary results address operating time. They do not by themselves resolve every aspect of the broader objective, and the interpretation of the cosmesis score depends on scale details that are not reported in the registry record.

3. Trial Design

The registry describes a randomized, single-masked, parallel-group trial of two skin-closure approaches for women undergoing cesarean delivery. Participants were assigned to absorbable staple wound closure using the INSORB device or suture wound closure using Monocryl. The registry lists enrollment as 117. The reported group summaries for the primary outcome include 59 participants in the suture group and 56 in the staple group; those are the outcome denominators in the posted results, not a reconciliation of all enrollment or follow-up.

The trial is listed as terminated. Its recorded start date is 2021-11-16 and its primary completion date is 2023-12-31. The reason for termination, the timing of the termination decision, and whether the study stopped before its intended recruitment or follow-up targets are not reported in the registry record. The listed phase is NA. The sponsor is The University of Texas Medical Branch, Galveston.

Single masking indicates that the registry reports masking, but it does not identify who was masked. Whether participants, clinicians, outcome assessors, or analysts were masked is not reported in the registry record. The registry also does not describe concealment of allocation, stratification, or other assignment procedures. Although the design is randomized, the posted record does not provide a detailed account of how randomization was implemented.

The primary endpoint is a continuous measure summarized by group means and standard deviations. The posted primary comparison is an unadjusted mean difference with an interval estimate and an unadjusted p value. The registry does not report the original sample-size justification, the trial's intended analysis populations, or a detailed statistical analysis plan. Those omissions limit assessment of how the completed study compares with its planned design.

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.

Before assignment: A total of 117 participants signed the consent, 2 participants withdrew. The study terminated early due to the low accrual.

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.

6. Primary Endpoint

The registry lists the primary outcome as Operating Time, measured over Start of surgery through end of skin closure in minutes.

The primary endpoint is operating time in minutes, defined as the time from the start of surgery through the end of skin closure. The registry describes it as total time for the procedure. It is therefore a broader measure of elapsed procedure time than skin-closure time alone: it includes the specified interval beginning at surgery start and ending when skin closure is complete.

Operating time is useful for comparing procedural duration because it is a continuous outcome that can be summarized by a mean and standard deviation in each group. A difference in group means describes the average contrast in recorded time. The standard deviations indicate how dispersed individual times were around each group's mean; they are not uncertainty intervals for the means.

The endpoint is relevant to the registry's stated objective of assessing operative time, but its interpretation should stay tied to its definition. It does not isolate the time spent applying the closure method, nor does it establish why any observed difference arose. The registry lists skin closure time in minutes as a secondary outcome, which is conceptually more specific to closure itself, but a numerical result for that outcome is not reported in the posted secondary results.

The posted group means are 69.2 minutes for suture closure and 61.9 minutes for staple closure. The reported mean difference is -7.3 minutes for absorbable staples relative to suture. This is a descriptive contrast from the posted group summaries; it should not be read as a guaranteed change for an individual procedure or as evidence about outcomes not measured by operating time.

7. Results Posted in the Registry

• Absorbable Staple Wound Closure: mean 61.90 versus 69.20 on control; difference -7.30 (95% CI -15.51 to 0.91), standardized effect d = -0.32; z-test p = 0.081.

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.

Wound Cosmesis

• 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:
  • Absorbable Staple Wound Closure: mean 3.20 versus 3.90 on control; difference -0.70 (95% CI -1.32 to -0.08), standardized effect d = -0.64; z-test p = 0.028.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Absorbable Staple Wound Closure than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Composite Wound Complication

• 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:
  • Absorbable Staple Wound Closure: 3.6% (2/56) versus 0.0% (0/59) on control; risk difference 3.6 percentage points (95% CI -1.3 to 8.4); unadjusted two-proportion z-test p = 0.143.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Absorbable Staple Wound Closure and the control. The interval gives the range of effects that remain compatible with the data.

Post Operative Pain

• 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:
  • Absorbable Staple Wound Closure: mean 0.70 versus 0.90 on control; difference -0.20 (95% CI -1.00 to 0.60), standardized effect d = -0.10; z-test p = 0.626.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Absorbable Staple Wound Closure and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results cover different dimensions of the closure question: wound appearance, composite wound complications, and postoperative pain. Their pattern is not uniform. The cosmesis comparison has an interval that excludes zero, while the wound-complication and pain intervals include zero. The registry also lists use of resources, adverse events, and skin-closure time among secondary outcomes, but numerical comparative results for those measures are not reported in the posted secondary summaries. These results therefore offer only a partial view of the secondary questions named in the record.

These outcomes complement the primary operating-time result rather than answer the same question. A difference in total operating time does not imply a corresponding difference in wound appearance, complications, or pain. Likewise, a secondary outcome cannot establish the primary procedural-time result. The cosmesis scale's direction and interpretation are not reported, so the numerical difference cannot be translated into a claim about better appearance. The event and pain outcomes also have uncertainty intervals that leave room for no difference.

Unadjusted secondary findings carry less weight because the registry does not report a multiplicity plan, and it lists no reported analyses for the secondary outcomes. When several outcomes are examined, a result that appears unusual can arise by chance, even if there is no underlying effect. Without a prespecified hierarchy or adjustment strategy, the secondary p values should not be treated as confirmatory evidence in isolation.

There are also differences in the number of participants contributing to the posted secondary outcomes. The registry does not explain those denominators or report how missing observations were handled. Consequently, comparisons across endpoints may reflect not only different outcome constructs but also different available data. Taken together, the secondary results add context, but they do not resolve the uncertainty around the primary comparison or fill in outcomes without numerical results.

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

• Wound Cosmesis
• Number of Participants With Composite Wound Complication
• Post Operative Pain
• Number of Adverse Events
• Use of Resources
• Skin Closure Time in Minutes

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, so its group summaries use means and standard deviations. A mean represents the average recorded operating time within a group. A standard deviation describes how spread out individual recorded times are around that mean. It is not the standard error and does not show how precisely the group mean or the between-group contrast has been estimated.

What does the mean difference express?

The reported primary mean difference is -7.3 minutes for absorbable staple closure relative to suture closure. In a difference defined as staple minus suture, a negative value means the observed staple-group mean is lower. This describes the direction and size of the difference between the posted group averages. It does not say that every participant's procedure was shorter, and it does not identify which parts of the measured interval account for the contrast.

A comparison of means is most straightforward to interpret when the outcome is measured consistently and the analysis appropriately reflects the study design. Random allocation supports a between-group comparison, but it does not remove the need to examine implementation, missing outcomes, and the prespecified analysis. Those details are not fully described in the registry record. The posted estimate is an unadjusted comparison based on summary statistics.

How should the interval be read?

A confidence interval conveys uncertainty around an estimated effect. Its endpoints mark a range of effect values reasonably compatible with the data and the method used, under the method's assumptions. It does not mean that the true effect has a particular probability of falling inside the observed interval. For the primary mean difference, the interval from -15.51 to 0.91 includes zero. Zero is the value corresponding to no mean difference. Thus the interval leaves open both a negative contrast and a small positive contrast, as well as no difference.

The interval and the p value answer related but different questions. The p value of 0.081 describes how incompatible the observed data are with a null model of no difference, under the assumptions of the test used. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The registry labels the comparison unadjusted and does not report a full analysis plan, so interpretation should not imply that the posted p value accounts for all possible design features or multiple outcomes.

Why do standard errors matter?

A standard error describes the sampling uncertainty of an estimated statistic, such as a group mean. The registry reports standard errors for the primary means, alongside their standard deviations. Standard errors are generally smaller when an estimate is more precise, while standard deviations reflect variation among observations. They answer different questions. A reader should not mistake the standard deviation for the uncertainty around the mean difference.

The reported comparison also includes a pooled standard deviation and a standardized effect size. A pooled standard deviation combines variability information across groups for purposes of expressing a difference on a common scale. A standardized effect expresses the mean contrast relative to that variability. These quantities can help compare effects measured on different scales, but they do not replace the original-unit estimate. In this trial, minutes remain the direct unit for the primary operating-time outcome.

What does an unadjusted comparison leave out?

An unadjusted comparison uses the posted group summaries without accounting for additional covariates or other model terms. That makes the arithmetic relatively transparent, but it may not match an analysis that adjusts for prespecified factors or handles the design in another way. The registry lists no reported analyses for the primary outcome. It does not report whether the trial's own analysis used covariate adjustment, how missing observations were handled, or which analysis population was intended. These absences prevent a complete assessment of the distinction between the posted recalculation and any analysis conducted by the investigators.

The record does not flag a discrepancy between the posted values and the recalculated comparison. That does not supply missing details of the statistical plan. If a sponsor analysis is not reported, the posted unadjusted estimate should be treated as a summary-based comparison rather than as a full account of the trial's inferential analysis.

Why can over-dispersion matter?

For continuous outcomes, variability is visible in the standard deviations. For count or binary outcomes, a statistical model may also need to allow for variability beyond what a simple model assumes. Over-dispersion means that observed variation is greater than a model expects; ignoring it can make uncertainty appear too small and can distort inferential conclusions. This is a general statistical issue, not a reported finding about this trial. The posted wound-complication outcome is a participant count by group, and the registry does not report a model-based analysis or a detailed method for that comparison.

For binary outcomes such as whether a participant had a composite wound complication, a risk difference compares the observed proportions between groups. The posted risk difference is 0.036 for staples relative to suture, with an interval from -0.013 to 0.084. Because the interval includes zero, the summary does not provide a precise distinction from no risk difference. With sparse event counts, estimates can be especially uncertain; the registry's posted comparison should therefore be read with its interval rather than as a categorical finding.

Multiplicity is another general concern when a trial evaluates several outcomes. Looking across multiple comparisons increases the chance that at least one result appears notable by chance, unless the analysis plan addresses that issue. The registry lists several secondary outcomes but does not report a multiplicity strategy. The secondary p values are unadjusted, and there are no reported secondary analyses. They should therefore be treated as exploratory evidence rather than as a set of independently confirmatory tests.

11. Confidence Intervals and Precision

The primary mean difference is -7.3 minutes, with an interval from -15.51 to 0.91 minutes. The interval extends across zero, the value for no mean difference, and covers contrasts in both directions. This means the posted data do not pin down the primary contrast to a narrow range. The point estimate gives a single best estimate under the calculation used, while the interval shows substantial uncertainty around that estimate.

Precision depends on the amount of information available and on variability in the outcome. The primary group standard deviations are 23.7 minutes for suture closure and 21.2 minutes for staple closure. These describe variation among observed times, not uncertainty in the group contrast. The group sizes for this outcome are 59 and 56, respectively. The registry does not report missing-data handling or explain why the endpoint denominators differ from the enrollment figure, so the available information does not show how the observed records relate to all enrolled participants.

The p value of 0.081 does not replace the interval. A p value compresses evidence into a single measure relative to a null model, whereas the interval shows both the direction and range of effect values compatible with the data and method. Neither measure determines whether a difference would matter in practice; that requires a relevant threshold or contextual judgment, which is not reported in the registry record.

The secondary intervals also illustrate varying precision. The cosmesis interval excludes zero, while the intervals for wound complications and postoperative pain include zero. These contrasts have different scales and meanings, and the cosmesis score direction is not reported. The results should not be compared only by which intervals cross zero: sample availability, outcome variability, scale properties, and the number of comparisons all affect interpretation.

Confidence intervals communicate sampling uncertainty under their method's assumptions. They do not account automatically for unreported sources of bias, missing outcomes, protocol deviations, or selective reporting. The registry's limited reporting of analysis methods and participant flow leaves those additional uncertainties unresolved.

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 original trial's design calculation. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The registry does not report the trial's own original design assumptions or sample-size justification.

For these continuous outcomes, the entries are participants per arm, not a total across both groups. The 80% power column represents a planning target under which a study designed with the stated assumptions would have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher chance of detection as its target. Neither column describes what happened in the completed trial.

Rows that plan for 100% of the observed effect use the observed estimate as the effect to detect; rows planning for 75% or 50% use smaller effects. Smaller effects are harder to distinguish from random variation, so the planning figures rise as the assumed effect becomes smaller. The resulting participant requirements also depend on the observed variability and the illustration's assumptions. Because the observed effect is uncertain, these figures should not be treated as a validated prediction of what a future study would require.

The curve and the accompanying figures are planning aids: they show how the illustrative participant requirement changes with the assumed effect size. They are not evidence that the completed study had adequate or inadequate power, and they do not establish the design the investigators originally intended. This is not observed power; it is a prospective calculation using an effect estimated from the posted results.

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 = -7.300; pooled standard deviation σ = 22.518.
2. n = 2 × (1.96 + 0.842)² × 22.518² / -7.300² = 149.4, rounded up to 150 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 <- -7.3                      # observed difference in means
sigma <- 22.5178827656551                     # 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(5112640)
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 = 150 (80% power), 200 (90% power)
 75% of observed effect: n per arm = 266 (80% power), 356 (90% power)
 50% of observed effect: n per arm = 598 (80% power), 800 (90% power)
power.t.test: 150.3 
Simulated power at n = 150 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes in addition to the primary operating-time endpoint. Testing or estimating multiple outcomes raises a multiplicity concern: the more comparisons considered, the greater the opportunity for at least one apparently notable result to arise by chance. A prespecified outcome hierarchy, an adjustment for multiple testing, or a clear exploratory designation can help readers interpret that situation. A multiplicity strategy is not reported in the registry record.

The posted secondary comparisons are unadjusted, and the registry lists no reported analyses for those outcomes. The record does not say whether the investigators considered multiplicity in their own analyses, whether any outcomes were designated as confirmatory, or whether the reported endpoints followed a prespecified hierarchy. Thus, the secondary p values should not be interpreted as if each were the sole planned test.

Missing-data handling is also not reported. The numbers contributing to outcome summaries differ across endpoints, while the registry's enrollment entry is 117. The record does not explain the reasons for these differences, describe participant flow by outcome, or state whether observations were excluded, unavailable, or analyzed under any imputation procedure. It would be inappropriate to infer why a particular denominator is smaller or to assume that missingness was unrelated to outcomes.

The intended analysis populations are not described. The registry does not state whether the primary comparison was planned for all randomized participants, a treatment-received population, or another defined group. It also does not report whether participants were analyzed according to their randomized assignment or how deviations from assigned closure were handled. Randomization supports a clear treatment comparison when preserved in analysis, but the relevant analysis details are not reported.

The trial's original sample-size justification, interim-analysis plans, and full statistical analysis plan are not reported in the registry record. The planning illustration based on the observed effect is not a substitute for those trial-specific details. Without them, it is not possible to assess whether the reported endpoint and analysis choices were prespecified, how early termination affected the planned design, or whether selective outcome reporting is a concern. These are limits of the available record, not proof that a particular analysis procedure was or was not performed.

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.

The registry's adverse-event summary lists zero serious adverse events affecting participants in the suture group and zero in the absorbable staple group. It also lists zero participants affected by other adverse events in each group, and zero deaths in each group. These are the figures recorded in the registry for the listed group risk sets.

Those entries should be read as reported counts, not as proof that either approach has no safety risk. A zero count in this trial does not establish that an event cannot occur, and it does not show how frequently events might occur in a broader population. The registry does not provide further event descriptions in the serious-event terms list, which is empty, or details about the event definitions, surveillance procedures, severity grading, or adjudication.

The registry also lists number of adverse events among the secondary outcomes, but the posted group safety summary does not provide a broader account of event types or comparative statistical analysis. The recorded figures describe what appears in this safety summary; the record does not report enough detail to make a comprehensive safety assessment or to compare risks precisely.

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

The primary result is an estimate of the difference in average operating time between the two closure groups in this randomized trial. The posted means were 69.2 minutes for suture closure and 61.9 minutes for absorbable staple closure, with a reported mean difference of -7.3 minutes for staples relative to suture. The interval from -15.51 to 0.91 minutes includes no difference and values in either direction. The p value is 0.081. Together, these statistics describe an observed numerical contrast with uncertainty; they do not establish a definitive effect.

The result does not show that every procedure would take less time with one method, nor does it isolate the time spent performing skin closure. The primary measure spans the start of surgery through the end of skin closure. The registry names skin-closure time separately as a secondary outcome, but a numerical result for that measure is not reported in the posted secondary summaries.

The result also does not determine whether wound cosmesis, complications, pain, resource use, or other outcomes differ in a meaningful way. Selected secondary comparisons are posted, but some intervals include zero, the cosmesis scale's direction is not reported, and other named outcomes lack numerical comparative results. The adverse-event summary records zero affected participants in each group, but that does not demonstrate absence of risk.

The trial's terminated status and the lack of reported termination reasons, analysis populations, missing-data methods, and original sample-size justification constrain interpretation. The record does not establish whether termination altered the planned enrollment or analysis. Nor does the posted comparison indicate how results might generalize beyond the women and settings represented in the trial.

A sound reading separates the observed estimate from a claim of proof. The registry provides useful descriptive and comparative statistics, but the uncertainty interval, missing design details, and incomplete outcome reporting leave substantial questions open. No treatment recommendation follows from these data alone.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through both its point estimate and its uncertainty. The mean operating-time contrast is easy to state, but the interval crosses zero and extends across a range of possible differences. Reporting only the group means or the p value would conceal important information about precision and the range of effects compatible with the posted data.

It also shows the distinction between an outcome aligned with the broad objective and a more specific procedural measure. Total operating time spans the start of surgery through skin closure, whereas skin-closure time is listed separately. That distinction matters because a comparison of overall duration cannot identify which procedural component accounts for a difference. When the more specific outcome lacks posted numerical results, the interpretation of the broader endpoint remains limited.

The record further demonstrates why secondary outcomes require context. Appearance, complications, pain, resources, adverse events, and closure time address different questions. A notable-looking unadjusted secondary result does not become confirmatory simply because it appears alongside a randomized primary comparison. Multiplicity planning and complete reporting help readers distinguish primary evidence from exploratory patterns, but those details are not reported.

Finally, registry status and data completeness affect statistical interpretation. The trial is listed as terminated, yet the reason is not reported; outcome denominators differ, yet missing-data handling is not described; and an original sample-size justification is absent. These gaps do not erase the posted estimates, but they limit what can be concluded about design adequacy, precision, and the relationship between planned and reported analyses. The example underscores that transparent reporting is part of interpreting an effect estimate, not an administrative detail separate from statistics.

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 information available for this trial. First, the trial is listed as terminated, but the reason for termination and its timing relative to the planned study course are not reported. The record therefore does not show whether termination affected recruitment, follow-up, or the analysis plan.

Second, the enrollment entry and outcome-specific denominators do not match across the posted results, and the registry does not explain participant flow or missing observations. The primary outcome includes 59 participants in the suture group and 56 in the staple group. The secondary outcome denominators vary further. Without reasons for those differences or a missing-data strategy, the representativeness of each endpoint's available observations cannot be assessed from the registry record.

Third, the registry does not report the original sample-size justification, the intended analysis populations, a detailed statistical analysis plan, or an interim-analysis plan. It also does not report who was masked despite listing single masking. These omissions prevent readers from checking whether the posted comparisons align with prespecified methods.

Fourth, the posted comparisons are unadjusted summary-based calculations, and the registry lists no reported analyses for the primary or secondary outcomes. The trial's own inferential methods are therefore not fully available for comparison. The secondary outcome list is broader than the numerical secondary results, and the meaning and direction of the wound-cosmesis scale are not described. These gaps limit interpretation of both outcome coverage and the practical meaning of score differences.

Finally, a single trial's posted estimates do not establish how results would apply in other settings. The registry record does not give enough detail about eligibility, participant characteristics, or clinical context to assess broader applicability. These limitations concern reporting and scope; they should not be mistaken for proof that the underlying trial procedures were inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Subcuticular Absorbable Staples Versus Conventional Skin Closure in Women Undergoing Cesarean Delivery — NCT05112640.
• Registry record last updated 2024-08-21; status last verified 2024-07.
• Results first posted 2024-08-21.
• 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 record describes a randomized, single-masked, parallel-group trial comparing absorbable subcuticular staple closure with Monocryl suture closure in women undergoing cesarean delivery. It lists enrollment as 117 and status as terminated. The primary outcome is operating time from the start of surgery through the end of skin closure.

Mean operating time was 69.2 minutes with suture closure and 61.9 minutes with staple closure. The reported unadjusted mean difference was -7.3 minutes, with an interval from -15.51 to 0.91 and an unadjusted p value of 0.081. Selected secondary results cover wound cosmesis, composite wound complications, and postoperative pain. The registry lists zero serious adverse events, zero other adverse events, and zero deaths in each group.

The reason for termination, original sample-size justification, analysis populations, missing-data methods, multiplicity strategy, and detailed statistical plan are not reported in the registry record. The posted comparisons are therefore best read as estimates from the available summaries, with uncertainty and reporting limitations kept in view.