Groin wound complications

The single most important thing about this paper, for this wiki, is what is not in it. The word "Szilagyi" does not appear anywhere in Labib 2026 — not in the Methods, not in any forest plot, not in the GRADE table, not in the Discussion. There is no deep-versus-superficial split of any kind: no CDC superficial/deep/organ-space stratification either. The outcome is surgical site infection as each included trial defined it, pooled undivided.

So Labib does not disagree with Gombert. It is silent. The wiki's groin depth limit — that the demonstrated prophylactic benefit is superficial, on Gombert 2020's Szilagyi II p = 0.46 and Szilagyi III p = 0.07 — is not challenged by this paper and stands unchanged. An updated meta-analysis that adds four trials and doubles the sample would have been the natural place to resolve the depth question with more power; it was not attempted, and that absence should be recorded rather than glossed. Nothing here permits a claim that closed-incision NPWT prevents deep or graft-involving groin infection.

What it does report. Ten randomised trials, 1,449 patients, 1,681 inguinal incisions.

Every arm total and event total reconciles. The twelve forest-plot rows sum to 826 and 855 incisions and to 89 and 179 events, matching the printed totals and the printed percentages exactly. The subgroup plots reconcile too: diabetes 78 and 65, 12 and 22 events; overweight 116 and 113, 19 and 43 events. The forest plots carry no text layer in the published PDF and were recovered by optical character recognition of the figure images, then re-added by hand.

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CAT: OCEBM 1 · START HIGH — a systematic review of 10 randomised trials in exactly the population this wiki is asked about, inguinal arterial surgery. For the overall SSI estimate: −1 risk of bias. The review's own RoB 2 grades two of ten trials at high risk and two with moderate concerns; four of the ten are open-label trials whose outcome is a clinician judgement of infection; and the pooled analysis is at INCISION level while randomisation in three of the trials was WITHIN PATIENT, so 1,681 incisions from 1,449 patients are treated as independent and the confidence interval is narrower than the data license. The authors concede the unit-of-analysis issue and state that a sensitivity analysis excluding clustered data did not change the result, but that analysis is not shown. NO downgrade for inconsistency (I² = 23%), indirectness (the population is the one being asked about) or imprecision (RR 0.53, 95% CI 0.40 to 0.71, 268 events). NET MODERATE — which is also the review's own grade, and the wiki agrees with it. For the two subgroups the wiki is more severe than the paper. Both rest on three trials only, and in both, ONE TRIAL — Gombert 2018 AIMS — carries 45.9% of the diabetic weight and 55.8% of the overweight weight. The diabetic subgroup has 143 patients and 34 events; the overweight subgroup 229 patients and 62 events. In the diabetic subgroup the AIMS arms are 42 against 22, a two-to-one imbalance inherited from a baseline diabetes prevalence of 43% against 24% in the parent trial — so the largest contributor to the diabetic estimate is a post-randomisation subset that is itself unbalanced. The overweight subgroup is not one population but three definitions pooled: Engelhardt contributed patients with BMI ≥ 30, the other two BMI ≥ 25, and the paper says so. −1 risk of bias, −1 imprecision. Net low for both, where the paper grades diabetes Moderate and overweight Low. The direction is not in doubt and should be said plainly: every one of the twelve overall forest-plot rows favours ciNPWT or is null, none favours the standard dressing, and the estimate sits on top of three independent predecessors. What is uncertain is the SIZE of the subgroup effects, not their existence. What this review cannot be graded on at all is depth: it reports no Szilagyi stratification and no deep-versus-superficial split of any kind.

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Nothing moves. Not infection, not dehiscence, not lymph leak, not seroma, not readmission, not reoperation, not stay, not quality of life. The only nominal signal in the trial is the EQ-5D self-care domain at 30 days, 2.1 with ciNPT against 2.2 with gauze, P = .04 in Supplementary Table I — one result among roughly twenty-one unadjusted comparisons, and the main text states that quality of life was similar "across all domains".

CAT: OCEBM 1 · This is the largest randomised test of ciNPT over a vascular groin incision and it is a null result whose point estimate favours plain gauze. Primary composite 37/115 (32.2%) with ciNPT against 33/119 (27.7%) with gauze, recomputed RR 1.16 (95% CI 0.78 to 1.72), risk difference +4.4% (−7.3 to +16.2). Surgical site infection 14/115 (12.2%) against 15/119 (12.6%), RR 0.97 (0.49 to 1.91). Multivariable OR 1.5 (0.82 to 2.75) in Table IV, printed as 1.4 (0.8 to 2.6) in the abstract; both sit above 1.0. Nothing separated the arms on dehiscence, lymph leak, seroma, readmission, return to theatre, adverse events, length of stay or EQ-5D. The power calculation is the key to what this trial does and does not settle: 121 per arm was chosen to detect a fall from 40% to 20%, a halving. The trial excludes a halving. It does not exclude the roughly 40% relative reduction in SSI that the pooled literature claims — its own SSI interval runs from 0.49 to 1.91, and the composite interval still admits a 22% relative reduction. Certainty is Moderate rather than High for the halving question because of unblinded outcome assessment, a 30-day horizon that misses late graft infection, and unresolved denominator confusion (four different arm-size pairs appear across the CONSORT diagram, Table II, Table III and Table V). Certainty for the SSI question is Low, downgraded twice for imprecision. It is NOT downgraded for sponsorship: the trial was funded by the device manufacturer and reported no benefit, so any residual sponsorship bias runs against the null and makes the null more credible.

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The two secondary claims that this paper is most often cited for — that ciNPT reduces reoperation and readmission — do not reach conventional significance on recomputation. Both point estimates run the right way, both intervals cross 1.0, and both are underpowered. Sorour 2022 and several reviews cite Kwon's reoperation and readmission reductions as established; this library records that they are not.

CAT: OCEBM 2 · The effect is large and survives recomputation; the published p-values do not. Major wound complication 5/59 (8.5%) against 15/60 (25.0%), RR 0.34 (95% CI 0.13 to 0.87), absolute reduction 16.5 percentage points, number needed to treat about 6. But the trial names its own test — the N−1 variant of Pearson chi-square via MedCalc — and applied to the printed cells that test returns P = .016 for the primary, not the P = .001 printed in the abstract, the Results and Table III. The identical p = .001 is printed against three different 2x2 TABLES (any complication, infection, major complication), which is arithmetically impossible; recomputed they are .042, .136 and .016. The two secondary claims this paper is most often cited for do not hold: reoperation recomputes to P = .117 against a printed P < .05, and readmission to P = .096 against a printed P < .04. Certainty is downgraded to Low for risk of bias (no blinding of any kind, with a treatment-driven outcome definition decided by unblinded surgeons; coin-toss allocation with no concealment mechanism; 40% of analysed incisions paired within 24 patients and analysed as independent units with no clustering adjustment) and for imprecision (20 events in total, trial stopped early for benefit at 80% of its planned sample, which systematically inflates the estimate). It is NOT downgraded for indirectness — the population is exactly the high-risk vascular groin a South African practice operates on — and NOT for publication or sponsorship bias: the trial was run without any support from the device manufacturer. The cost claim is Very low: a $6,045 saving at P = .11, from a distribution whose standard deviation exceeds its mean and whose range reaches $192,658, tested with a two-sample t test.

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What was done. A trial sequential analysis of the primary outcome, surgical site infection, run in Trial Sequential Analysis Software 0.9.5.5 beta from the Copenhagen Trial Unit. Type I error was controlled by adjusting the Z-value thresholds with the O'Brien-Fleming alpha-spending function; Z-values were further penalised according to the law of the iterated logarithm for the strength of the available evidence and the number of repeated significance tests; type II error was controlled with a beta-spending function and futility boundaries. Two-sided, 95% confidence level. The information size was estimated at 80% power and 5% type I error, with the event proportions in each arm derived from a proportion meta-analysis — the pooled proportion taken as the back-transformation of the weighted mean of the transformed proportions.

The three numbers that matter.

What the authors concluded from it, verbatim: "Therefore, it can be inferred that negative pressure wound therapy is superior to the control intervention. The existing evidence can be considered to be conclusive, and no further trials to assess this outcome are required."

In plain terms. A trial sequential analysis asks whether a meta-analysis has accumulated enough information to justify the confidence its p-value advertises, given that the p-value has been recomputed every time a trial was added. The monitoring boundary is a moving, conservative significance threshold that starts very high when little data has accrued and relaxes towards the conventional 0.05 as the required information size is approached. Crossing it before the required information size is reached is the strongest positive result the method can give: it says the effect is large enough that the evidence became conclusive early, and that random error is not a plausible explanation for it. That is what happened here, on the second of six cumulative tests, and the data then went on to exceed the required information size by more than threefold.

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CAT: OCEBM 1 · START HIGH — a systematic review of randomised trials in exactly the population this wiki is asked about, the vascular groin. −1 risk of bias. Blinding of participants was impossible in all six trials; blinding of outcome assessment was clearly reported in only two and was unclear or absent in four; reporting bias was rated HIGH in three of six by the review's own assessment; allocation concealment was not described in three; one trial was commercially funded and rated high risk for other bias; and one contributor is a conference abstract whose risk of bias could not be assessed at all. −1 imprecision and fragility as an answer to the present question. The estimate rests on 148 events. Every one of the six trials was published 2016-2018, and the three randomised trials published afterwards — Bertges 2021, Rodríguez Lorenzo 2024 and Daryapeyma 2025 — are individually null, so the pooled relative risk in labib 2026 inguinal cinpwt updated meta is 0.53 where this one is 0.36. An estimate that moves by a third when the evidence base doubles was not as settled as its trial sequential analysis declared. NO downgrade for inconsistency (I² = 0%) or indirectness. NET LOW for the question a 2026 motivation asks. If the claim is narrowed to 'the six trials available in 2018 showed a large and statistically robust reduction', that claim is MODERATE and is not in dispute. The depth strata are graded separately and lower. Szilagyi I, OR 0.40 (0.24-0.69) on four trials and 568 wounds, loses significance when Gombert 2018 is removed: −1 risk of bias, −1 imprecision, NET LOW. Szilagyi II, OR 0.51 (0.25-1.04), and Szilagyi III, risk difference −0.03 (−0.05 to 0.00), are both null AND both become significant when a single trial is removed: −1 risk of bias, −2 imprecision, net very low. The nulls are too fragile to be quoted as evidence of absence, and too suggestive to be dismissed.

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• Median age 75; 70% operated for lower-limb ischaemia; intestinal flora in 88% of wound cultures.
• Median VAC duration 20 days; 27/33 (82%) wounds healed within 55 days.
• One serious VAC-associated bleeding and three late false femoral aneurysms.
• Median cost of VAC treatment was 2.7% of total in-hospital costs.
• Synthetic vascular graft infection (n=21) was associated with adverse infection-related events (n=9; p=0.012); non-healing SSI was associated with amputation (p=0.005) and death (p<0.001).

CAT: OCEBM 4 · The headline this wiki has been quoting does not reproduce. The abstract states that '27 (82%) wounds healed within 55 days'. Table 2 gives time to full skin epithelialisation as a MEDIAN of 55 days with a range of 25 to 217 days, among the 27 wounds that healed. Half of the healed wounds took longer than 55 days and one took 217. The abstract has restated its own median as a deadline, and both this CAT and the evidence page have carried that wording. A SECOND UNDERCOUNT. The abstract reports 'one serious VAC associated bleeding'. The Results section, under its own heading, describes TWO VAC-associated bleeding events in two patients: one severe, with circulatory instability and a litre of blood in the canister from a disrupted infected vein patch requiring emergency vein interposition and a sartorius flap; and one with moderate arterial bleeding of unidentified source that ended VAC therapy and required coiling of the superficial femoral artery and a stentgraft. The correct denominator is 2/33 (6.1%) VAC-associated bleeds, of which 1/33 (3.0%) was severe. A THIRD ERROR. The Results text reads 'Almost half, 14/23 (42%) of the infected groins were in patients with diabetes mellitus'; 14 of 23 is 61%, and Table 3 gives diabetes as 14 (42%), which is 14 of 33. The printed denominator in the text is wrong. What does reproduce: healing 27/33 (82%); median VAC duration 20 days (range 3 to 119); dressing changes median 7 (1 to 40); treated outside hospital 16/33 (48%); intestinal flora 29/33 (88%); Enterococcus faecalis 12/33 (36%); Staphylococcus aureus 5/33 (15%); inadequate initial antibiotic therapy 18/33 (55%); amputation 6/33 (18%); mortality 9/33 (27%); amputation-free survival 22/33 (67%); graft removal 4/24 (17%). Synthetic graft healing 15/21 (71%) against 12/12 (100%) for the rest, p = 0.06; composite infection-related adverse outcome 9/21 (43%), p = 0.012, though the components listed total 16 events across those 9 groins. The cost figure needs its denominator: VAC cost was 2.7% of in-hospital cost with a range of 0.6% to 9.9%, in the 15 patients WHO completed VAC in hospital, not in the series; median in-hospital cost was 26 022 euros and median total VAC cost 1299 euros, which is 5.0% of the median. Median follow-up 16 months; loss to follow-up not reported. No conflict-of-interest statement and no funding statement appears anywhere in the article.

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