Analgesic and Anti-Inflammatory Activity of Ambroxol in the Treatment of Endometriosis: An Experimental Study in Wistar Rats

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript investigates the potential analgesic and anti-inflammatory effects of ambroxol in an experimental model of endometriosis. The topic is relevant and the study is well designed, including multiple behavioral, biochemical, and histological outcomes. The manuscript is generally well structured and provides interesting data supporting the potential repurposing of ambroxol. However, several aspects could be clarified or improved to further strengthen the manuscript.

1. In the Introduction (p. 2, lines 67-76), the pharmacological properties of ambroxol are well described. However, the authors could further clarify what specifically distinguishes this study from previous experimental studies investigating the analgesic or anti-inflammatory effects of ambroxol.
2. In several figures (Figures 1-3, p. 3-5), the large number of statistical symbols and comparisons makes the graphs somewhat difficult to read. Simplifying the annotations or presenting some comparisons in supplementary material could improve clarity.
3. In the section describing IL-1β levels (p. 5, lines 157-164), the authors state that the 50 mg/kg dose was the most effective, reducing cytokine levels to near zero. However, the magnitude of this reduction appears substantially different from the other ambroxol groups. The authors may consider clarifying whether this reflects biological variability or methodological differences.
4. The Discussion section (pp. 10-12) contains several very long paragraphs. The authors may consider shortening or restructuring some sections to improve readability and emphasize the most relevant findings.
5. In p. 11, lines 272-276, the authors state that the absence of differences among doses indicates that the lowest concentration was sufficient to elicit a significant analgesic effect. The authors may consider clarifying whether this reflects a true dose-independent effect or a possible limitation related to sample size or statistical power.
6. In p. 13, lines 370-375, the sentence describing the study limitations is very long and contains multiple elements. Splitting this sentence into shorter statements could improve readability and clarity.
7. In the Methods section (p. 14, line 414), four animals reportedly died during anesthetic induction and were excluded from the study. It would be helpful if the authors could clearly specify the final number of animals included in each experimental group after all exclusions.
8. In the treatment protocol (p. 16, lines 497-504), the authors describe the use of allometric scaling to derive the ambroxol doses. The authors may consider briefly clarifying the rationale for selecting 100 mg/kg as the highest tested dose.

Comments on the Quality of English Language

 The English could be improved to more clearly express the research.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The study evaluates the analgesic and anti-inflammatory potential of ambroxol in an experimental model of endometriosis in Wistar rats. The pharmacological repurposing approach is interesting; however, I have several observations:

 Why was inhalational maintenance required after ketamine/xylazine induction?. Were anesthetic depth and oxygenation monitored?. Could the four anesthetic deaths be related to combined anesthetic burden?

The manuscript states that isoflurane was administered at “2.5% MAC.” MAC is a relative measure of anesthetic potency, not a percentage unit. Please clarify whether the animals received 2.5% isoflurane or 2.5 MAC, and revise terminology accordingly. Review throughout the manuscript.

Some abbreviations are defined at their first occurrence and then unnecessarily redefined later in the text. Please review the entire manuscript to ensure that each abbreviation is defined only once at first mention and used consistently thereafter

Figure 8 provides an illustrative depiction of the surgical procedure; however, as the endometriosis induction model is well established and adequately described in the Methods section, the figure may not be essential for scientific interpretation. The authors may consider moving it to the Supplementary Material to improve focus on experimental findings.

The final analyzed sample (n = 38) was lower than the a priori calculated sample size (n = 48) due to anesthetic mortality and exclusion of animals that did not develop cystic lesions meeting predefined criteria. This reduction in sample size may have affected the originally planned statistical power (80%) and the ability to detect intergroup differences, particularly for secondary outcomes or dose–response comparisons. The manuscript does not indicate whether statistical power was recalculated after these exclusions.

Although the authors state that doses were determined using allometric scaling, the manuscript does not specify the assumed human body weight used for conversion

the authors should clarify whether scoring for pain assessment was performed from live observation or recorded images, and whether animals were habituated prior to evaluation

Based on the equipment used (digital analgesimeter), it appears that the procedure corresponds to an electronic von Frey or dynamic aesthesiometer rather than the traditional filament-based von Frey method. Please clarify the exact methodology.

Additionally, the behavioral criterion used to define a “withdrawal” response is not specified. It should be clearly stated whether this corresponded to abdominal contraction, withdrawal of the abdomen, jumping, vocalization, or another defined response.

The description of the von Frey procedure states that stimuli were repeated up to six times; however, the manuscript does not clearly specify how the final withdrawal threshold was determined , and what inter-stimulus interval was used. Please clarify whether thresholds represent a single value, the mean of repeated trials, or a defined criterion.

The manuscript does not specify whether cytokine measurements were performed in duplicate or triplicate.

The statistical analysis section does not report whether assumptions of normality were evaluated prior to performing ANOVA. Please specify whether normality and homogeneity of variance were assessed, and justify the use of parametric tests accordingly. If assumptions were not met, the use of appropriate non-parametric alternatives should be considered.

The sentence “This section is not mandatory but can be added to the manuscript if the discussion is unusually long or complex.” appears in the Conclusion section. This statement seems to be part of the journal template rather than content intended for publication. It should be removed from the manuscript, as it does not form part of the scientific text.

There is inconsistency in the nomenclature used to describe the treatment groups. In the main text, the group is referred to as “Abx100,” whereas in the figures it appears as “Abx 100.” Please standardize the nomenclature across the entire manuscript

In some sections of the manuscript, the authors state that no significant differences were observed among the experimental treatment doses. However, in other sections, the results are described as demonstrating a dose-dependent effect. These statements appear inconsistent.

The symbolic system used to denote pairwise comparisons in the figures requires clarification and possible revision. In the current format, asterisks (*, **) and other symbols (+, ++, etc.) are used to identify specific group-to-group comparisons rather than levels of statistical significance. However, in biomedical literature, asterisks are conventionally interpreted as graded indicators of statistical significance (e.g., *p<0.05, **p<0.01, ***p<0.001). Using one or two identical symbols (e.g., * vs **) solely to distinguish comparison pairs may lead to confusion or misinterpretation by readers. For example, a reader may incorrectly assume that ** indicates a stronger level of significance than *. Please, Improving the annotation system would enhance clarity and prevent misinterpretation of statistical results.

The manuscript shows variability in the von Frey sensitivity results within the Control (−) group across the evaluation period. Notably, the final assessment appears to show lower mechanical sensitivity compared to earlier time points. The authors should clarify how this temporal variation is explained. It is important to determine whether this reflects spontaneous attenuation of the model over time, adaptive behavioral responses, or methodological variability.

This pattern is particularly relevant because the strongest effects of ambroxol appear at the final time point. If the Control (−) group itself demonstrates partial recovery or reduced sensitivity at later stages, this temporal trend could influence the apparent magnitude of treatment effects. The potential interaction between time and treatment group should therefore be analyzed and discussed more thoroughly.

Additionally, the reference treatment was administered as a single dose, whereas ambroxol was given daily for 21 days. The manuscript does not provide sufficient pharmacological justification for this difference in dosing regimen. If progesterone was administered only once, it would be expected that its maximal effect would occur at earlier time points, corresponding to peak systemic concentration. However, the strongest reported effects appear at the final evaluation. The authors should clarify the pharmacokinetic rationale underlying this design and discuss whether the observed temporal pattern may be influenced by trends within the Control (−) group.

The manuscript reports alterations in motor coordination in the disease model. Given that endometriosis is primarily a visceral inflammatory condition, the mechanism by which the model induces measurable impairment in motor coordination requires clarification.

The reported serum IL-1β levels in the ambroxol-treated groups, particularly the 50 mg/kg group, appear markedly lower than those observed in all other groups, including the Sham group. The authors should clarify how this finding is interpreted biologically.

The Discussion attributes the observed effects to specific molecular pathways, including NF-κB, NLRP3, and related signaling mechanisms. However, the present study measured only serum IL-1β levels and total leukocyte counts, without directly assessing these molecular pathways. Therefore, mechanistic statements suggesting modulation of NF-κB, NLRP3, or other signaling cascades are not directly supported by the experimental data. I recommend reformulating these interpretations as hypotheses or potential mechanisms rather than demonstrated effects.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have addressed most of the comments; however, some important points that are necessary to provide stronger methodological support for the study remain insufficiently clarified.

The authors’ explanation is plausible; however, the justification remains insufficiently supported. If progesterone was administered only once, its maximal effect would generally be expected at earlier time points, whereas the strongest reported effects appear at the final evaluation. Please provide specific references documenting the pharmacokinetic and pharmacodynamic profile of medroxyprogesterone acetate for the route and regimen used, particularly with regard to delayed peak concentration and prolonged biological activity. In addition, please expand the discussion of the temporal response pattern, including whether the stronger effect observed at the final time point may have been influenced, at least in part, by the trajectory of the Control group, beyond the statistical significance detected by two-way ANOVA.

The use of two-way ANOVA is appropriate. However, the response remains only partially satisfactory because it does not clearly indicate whether the time × treatment interaction was statistically significant, nor does it fully address how the temporal decline in the Control group may have influenced the apparent magnitude of the late treatment effect. Please clarify this point explicitly in the results and expand the discussion accordingly.

Author Response

Please see the attachment.

Author Response File: Author Response.pdf

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

The revised manuscript adequately addresses the comments, and I have no additional observations.