Open-Label Prospective Randomized Comparative Study of the Efficacy and Safety of Gentamicin in Comparison to Other Antibiotics in the Management of Acute Appendicitis in Surgically Treated Patients

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Dear Authors,

 

Thank you for your valuable contribution to the literature, and to opportunity. 

Current study revealed a prospective randomized open-label clinical study comparing three antibiotic regimens—gentamicin plus metronidazole (GTM+MZ), ertapenem (ETP), and cefuroxime plus metronidazole (CXM+MZ)—in adult patients undergoing surgery for acute appendicitis. The study aims to evaluate both clinical efficacy and safety, including the assessment of renal injury biomarkers, which represents an interesting and relatively novel aspect of the work.

My suggestions: 

1. The authors describe the study as a prospective randomized open-label trial,  

However, several important aspects require clarification:

• The allocation concealment method is not described.

• It is unclear whether block randomization or stratification was used.

• The absence of blinding may introduce performance bias, especially in outcomes such as treatment duration or hospital stay.

2. The manuscript states that 2117 patients were admitted with appendicitis during the study period, but only 170 patients were randomized. 

 

But:

• A screening log was not collected.

• The reasons for exclusion of the majority of patients remain unclear.

This raises concerns about selection bias and external validity.

 

3. The gentamicin dose used (~3 mg/kg) is significantly lower than the EUCAST recommended 6–7 mg/kg dosing. 

This raises two issues:

• Potential underdosing

• Limited generalizability to institutions following modern dosing strategies

Recommendation

Authors should explain:

• The rationale for the lower dose

• Whether therapeutic drug monitoring was performed

• How this dose compares with international practice6. Clinical Outcomes

The primary outcomes include:

• duration of antibiotic therapy

• length of hospital stay

• CRP dynamics

• postoperative complications 

   

However, important surgical outcomes are missing, such as:

• intra-abdominal abscess

• surgical site infection rate

• readmission rate

• reoperation

 

Author Response

Dear Editor, der Reviewer,

 

please find attached the responses to the review.

 

Kind regards, Bojana Beović and Nika Obolnar

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Comments

This is a clinically relevant and pragmatic trial that tackles an important antimicrobial stewardship question: can a once-daily gentamicin plus metronidazole regimen perform as well as broader β-lactam–based regimens in adults undergoing appendectomy with adequate source control, while keeping nephrotoxicity acceptable? The inclusion of early kidney injury biomarkers in addition to classic renal parameters is a genuine strength. At the same time, several aspects of the design, outcome definitions and analysis currently limit how confidently we can interpret the comparative efficacy and safety results and, in particular, how far we can go in drawing stewardship conclusions.

1. A central concern is the choice and implementation of the primary outcome. “Clinical response” as you define it is largely driven by physician decisions: duration of antibiotic therapy, length of hospital stay, and CRP trajectories, all of which treating surgeons adjusted according to intraoperative impressions and clinical judgement. This inevitably introduces strong clinician-dependent variability and confounding by disease severity and by individual practice style, which makes it difficult to attribute any differences (or similarities) to the antibiotic regimen itself. I would strongly encourage you to re-anchor the trial around objective, protocol-defined clinical endpoints such as 30-day surgical site infection, intra-abdominal abscess, re-operation and readmission, ideally using standard criteria (CDC SSI definitions or similar). At minimum, you should provide analyses for these “hard” endpoints, stratified or adjusted for appendicitis severity (uncomplicated versus gangrenous/perforated, abscess, AAST grade), so that readers can see how outcomes compare at a similar level of disease.

2. Related to this, the Conclusions currently use “did not show inferiority” language, which implies a formal non-inferiority trial, but the study is neither designed nor analysed as such. There is no prespecified non-inferiority margin, no sample-size calculation based on that margin, and no confidence-interval-based NI inference. In its present form the trial is best described as an exploratory comparative study. I would recommend removing all “non-inferiority” wording or, if you wish to retain the spirit of that claim, rephrasing to something like “we did not observe clinically relevant differences in…” and presenting confidence intervals for the between-group differences, without implying that formal non-inferiority has been established.

3. The way randomization and allocation are implemented also deserves a more transparent handling. Generating the sequence with Excel and allowing enrolling personnel access to that sequence, combined with pre-prepared paper records assigning treatment that are used sequentially in the ED, creates a non-trivial risk of selection bias. Even if no intentional manipulation occurred, the possibility that clinicians could foresee upcoming allocations should be acknowledged. It would be important to describe, as clearly as possible, who generated the sequence, who had access, how envelopes or records were stored and opened, and how allocation was implemented in practice. It would also help to show that baseline indicators of disease severity (imaging, intraoperative findings, initial WBC and CRP, perforation or abscess rates) are balanced between groups, to reassure readers that any allocation bias is limited.

4. Another major limitation is the lack of a screening log and incomplete description of the recruitment funnel. You note that there were 2117 appendicitis admissions during the study period but only 170 patients were randomized, and that reasons for non-inclusion were not systematically recorded. Without at least a reconstructed screening profile, it is difficult to assess the representativeness of the trial patients relative to the broader appendicitis population. If possible, I would encourage you to retrospectively summarise the main exclusion categories (for example, paediatric age, non-operative management, language barriers, refusal, comorbidities) and to provide some basic demographic and clinical comparison between the randomized cohort and the overall appendicitis population at your centre(s).

5. The gentamicin dosing strategy also warrants careful reconsideration in a stewardship context. You used a fixed 240 mg once daily dose, which corresponds to roughly 3 mg/kg in an average adult and is explicitly lower than EUCAST-recommended 6–7 mg/kg once-daily dosing for serious Gram-negative infections. This raises concerns about whether optimal pharmacodynamic targets (Cmax/MIC) were consistently achieved, especially as resistance patterns evolve. I think it is important to provide the distribution of actual mg/kg doses based on recorded body weights, explain the rationale for choosing this specific fixed dose, and state whether any therapeutic drug monitoring (peak/trough levels) was performed, even in a subset. It would also considerably strengthen the stewardship message to show your local microbiology context: the institutional antibiogram for the main intra-abdominal pathogens during the study period, particularly aminoglycoside and cephalosporin susceptibility, so that readers can assess how generalisable your conclusions might be.

6. Your analysis of CRP dynamics highlights another area where the current approach is vulnerable. CRP values are missing in a substantial proportion of patients—around 30% for the first postoperative day and over 40% at discharge—and the ANOVA you report is based on only 78 complete cases. It is highly plausible that this missingness is not random (for example, patients discharged early or considered clinically well may have fewer blood tests), which means standard complete-case methods and simple EM imputation can be misleading. It would be helpful to tabulate CRP missingness by treatment group and by length of stay, and to consider mixed-effects models that can use all available CRP measurements while accounting for within-patient correlation. That said, I would also caution against placing too much weight on CRP trajectories, which are surrogates; the main clinical conclusions should rest on objective outcomes such as infection and reintervention rather than on inflammatory markers alone.

7. The complication analysis is underpowered and the statistical interpretation needs to be more cautious. With only five in-hospital complications overall, and only two infectious complications (both in the gentamicin arm), p-values will inevitably be unstable, and the borderline significance you report for “any complication” (p = 0.049) is not by itself compelling. In this setting, it is more informative to provide absolute event rates and risk differences with 95% confidence intervals rather than rely on dichotomous significance thresholds. For these sparse binary outcomes, simple methods such as Fisher’s exact test are preferable to over-parameterised count models. If possible, extending follow-up beyond one month (for example, to 90 days) and applying standardized definitions for surgical site infection and intra-abdominal sepsis would also add robustness to your safety and efficacy conclusions.

 

Author Response

Dear Editor, dear Reviewer,

 

please find attached the responses to the review.

Kind regards, Bojana Beović and Nika Obolnar

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Dear Authors,

 

Thank you providing a revised version of manuscript. The revised version shows clear improvement, especially in statistical reporting and structure of results.

However, there are still important methodological, reporting, and interpretation concerns that should be addressed before acceptance.

1. The open-label design introduces performance and detection bias, especially for subjective endpoints. 

• The sample size appears underpowered, particularly given the very low complication rate (≈6%).
• Authors themselves acknowledge this limitation, but:
  • No post-hoc power analysis is provided.
  • The study risks a Type II error (false negative equivalence).

Explicitly discuss the non-inferiority vs equivalence interpretation problem, and clarify that results should be interpreted as hypothesis-generating rather than definitive.

 

2. Randomization via Excel RAND() is acceptable but:

• • No mention of allocation concealment.
• Screening log not recorded → selection bias risk

Clarify:

• allocation concealment method,
• whether recruiters were blinded to assignment sequence.

 

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

Comments and Suggestions for Authors

The revised manuscript addresses every point I raised.

Author Response

Comments 1: The revised manuscript addresses every point I raised.

Response 1: Thank you very much for reading our paper and your comments.