Resistance Training Complements Anti-TNF Therapy in DSS-Induced Colitis by Improving Skeletal Muscle Inflammatory and Mitochondrial Gene Signatures

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The study addresses an interesting and clinically relevant question by exploring the interaction between resistance training and anti-TNF therapy in a DSS-induced colitis model. That said, there are several issues that limit how robust and interpretable the findings are, as well as how far they can be translated. Below are some points that should be addressed.

 

Title and Abstract

The statements that resistance training “reprograms muscle metabolism” and “potentiates therapy” are too strong for the type of data presented. The study shows associations, but not direct mechanistic evidence to support these claims.

The small sample size (n = 6 per group) is not acknowledged.

The suggestion of clinical applicability feels premature given that this is a preclinical model.

 

Introduction

The hypothesis is not clearly stated. It would help to frame it more directly and in a way that can be clearly tested.

The text tends to assume that resistance training is beneficial, without really discussing the limitations or inconsistencies in the literature, especially in the context of IBD.

The gap between rodent exercise models and human clinical settings is not sufficiently considered.

 

Materials and Methods

Experimental design

The sample size is small, and there is no mention of a power calculation.

Only male mice were used, which limits how broadly the findings can be interpreted.

Randomization is mentioned, but the details are minimal, particularly regarding allocation concealment.

There is no indication that functional assessments (e.g., grip strength, swimming) were performed in a blinded manner, which raises concerns about bias.

DSS model

The model is described as chronic, but the protocol appears to involve only a single DSS cycle, which is more consistent with a subacute model.

The use of three mice to “validate” the model before the main experiment is unconventional and does not add much from a statistical standpoint.

Interventions

The infliximab dosing and schedule are not sufficiently justified or referenced.

Outcome measures

The functional tests are appropriate but inherently operator-dependent, which reinforces the importance of blinding.

Using only three animals per group for histology is a clear limitation.

The transcriptomic analysis lacks important details (e.g., handling of batch effects, normalization, and number of biological replicates).

Statistical analysis

The use of the Bliss independence model is not well justified and is not standard in this type of study.

Multiple testing correction for transcriptomic data is not clearly described beyond stating FDR.

 

Results

The manuscript frequently refers to synergy or “potentiation,” but this is not supported by the statistical analyses. In most cases, there is no significant interaction in the two-way ANOVA. The data are more consistent with additive effects, and the text should reflect that.

The functional results are consistent across tests, but the interpretation tends to go a bit too far. It would be more informative to show clearly how much each group improves, rather than implying that the combination is clearly superior without direct statistical support.

 

Discussion

The idea of combining exercise with biologic therapy is interesting and worth exploring, but the discussion leans toward overinterpretation.

The lack of mechanistic experiments is not acknowledged.

Limitations of the DSS model are not discussed in enough depth.

The clinical implications are overstated given the preclinical nature of the work.

Key limitations, such as the small sample size and the use of only male animals, should be emphasized more clearly.

 

Conclusion

The conclusions are stronger than what the data support. Claims about clinical applicability should be toned down.

Overall, the findings suggest an association between resistance training and improved outcomes in this model, but they do not demonstrate a clear mechanistic interaction.

Author Response

We sincerely thank Reviewer 1 for the thorough and constructive evaluation of our manuscript. The detailed comments have substantially improved the rigor, transparency, and interpretability of our work. Below we provide a concise summary of the key revisions made in response to each comment. All supplementary changes in the revised manuscript are indicated in red font or by the corresponding line numbers.

 

Comments and Suggestions for Authors:

The study addresses an interesting and clinically relevant question by exploring the interaction between resistance training and anti-TNF therapy in a DSS-induced colitis model. That said, there are several issues that limit how robust and interpretable the findings are, as well as how far they can be translated. Below are some points that should be addressed.

Comment 1:

Title and Abstract: The statements that resistance training “reprograms muscle metabolism” and “potentiates therapy” are too strong for the type of data presented. The study shows associations, but not direct mechanistic evidence to support these claims. The small sample size (n = 6 per group) is not acknowledged. The suggestion of clinical applicability feels premature given that this is a preclinical model.

Response:

We sincerely thank you for your thoughtful and constructive evaluation of our manuscript. Your careful reading and insightful comments have been invaluable in helping us refine the presentation and interpretation of our findings. We greatly appreciate the time and effort you have dedicated to reviewing our work. Below, we address each of your concerns regarding the Title and Abstract in detail.

Point 1: The statements that resistance training “reprograms muscle metabolism” and “potentiates therapy” are too strong for the type of data presented. The study shows associations, but not direct mechanistic evidence to support these claims.

We fully agree with the Reviewer’s assessment and appreciate this important criticism. We recognize that our original phrasing overstated the direct mechanistic conclusions that can be drawn from the current data. As the Reviewer correctly points out, our transcriptomic, qPCR, and serum biomarker analyses reveal associations rather than establishing causality. In response, we have carefully revised the Title and Abstract to adopt more measured and evidence-appropriate language. Specifically, the Title has been changed to emphasize association and improvement rather than definitive reprogramming or potentiation with mechanistic certainty. Throughout the Abstract, we have replaced overly definitive verbs (e.g., “reprogrammed,” “potentiating”) with more cautious and correlational phrasing (e.g., “was associated with improved,” “suggesting that resistance training may enhance…”). These revisions ensure that the level of certainty in our language accurately reflects the associative nature of our evidence. We sincerely thank the Reviewer for this guidance. (Lines 13 to 30)

Point 2: The small sample size (n = 6 per group) is not acknowledged.

Thank you for raising this important limitation. We recognize that the small sample size is a relevant consideration when interpreting our findings. In response, we have integrated an explicit acknowledgment of the sample size into the revised Abstract (see below), noting that this study was conducted “in a relatively small cohort.” Additionally, we have ensured that the Discussion section of the revised manuscript (Section 4) includes a thorough consideration of sample size limitations. This limitation is now stated transparently, both in the Abstract and in the main body, to ensure readers can appropriately contextualize the generalizability of our results. We are grateful for this suggestion. (Lines 725 to 729)

Point 3: The suggestion of clinical applicability feels premature given that this is a preclinical model.

We appreciate this very reasonable caution. We agree that direct clinical translation from a preclinical mouse model is premature. Accordingly, we have significantly tempered the language in the Abstract regarding clinical relevance. Instead of implying immediate applicability, we now state that “incorporating structured resistance exercise may represent a strategy worthy of further investigation to improve biologic responsiveness in IBD patients with muscle loss.” This phrasing frames our findings as a hypothesis-generating basis for future clinical exploration rather than a finalized clinical recommendation. We believe this revised wording appropriately conveys the preliminary nature of our preclinical results while retaining the translational potential of our work. We thank the Reviewer for encouraging this important refinement.

 

Comment 2: Introduction

The hypothesis is not clearly stated. It would help to frame it more directly and in a way that can be clearly tested.

The text tends to assume that resistance training is beneficial, without really discussing the limitations or inconsistencies in the literature, especially in the context of IBD.

The gap between rodent exercise models and human clinical settings is not sufficiently considered.

Response:

We sincerely thank you for your insightful and constructive comments on our Introduction. We fully agree with your assessment and have made substantial revisions to address each point.

1. The hypothesis was not clearly stated.

Thank you for pointing this out. We have now added an explicit, testable hypothesis at the end of the Introduction (final paragraph), stating: “We hypothesized that progressive resistance training would enhance skeletal muscle mitochondrial oxidative phosphorylation, reduce systemic inflammation, and thereby improve the therapeutic efficacy of anti-TNF-α antibody treatment in a DSS-induced colitis mouse model.” This directly frames the study’s aim in a falsifiable manner. (Lines 71 to 78)

2. The text tended to assume resistance training is beneficial without discussing limitations or inconsistencies in the literature, especially in the context of IBD.

This is an excellent point. We have revised the Introduction to acknowledge that while resistance training has well-documented benefits in healthy individuals, its effects in chronic inflammatory states like IBD are less clearly defined. We now mention that some clinical observations suggest that intensive exercise may transiently worsen gastrointestinal symptoms in IBD patients, and that the optimal training modality, intensity, and duration have not been established in this population. This more balanced perspective better reflects the current evidence. (Lines 62 to 70)

3. The gap between rodent exercise models and human clinical settings was not sufficiently considered.
   We agree that this translational gap is an important limitation that should be acknowledged upfront. In the revised Introduction, we explicitly note that the ladder-climbing resistance protocol, though validated for inducing muscle adaptation in rodents, differs from voluntary human exercise in terms of engagement, loading patterns, and neural recruitment. We therefore caution that extrapolation to clinical practice should be done prudently, setting the stage for the cautiously worded conclusions in our manuscript. (Lines 71 to 78)

 

Comment 3: Materials and Methods

The sample size is small, and there is no mention of a power calculation. Only male mice were used, which limits how broadly the findings can be interpreted. Randomization is mentioned, but the details are minimal, particularly regarding allocation concealment.

There is no indication that functional assessments (e.g., grip strength, swimming) were performed in a blinded manner, which raises concerns about bias.

The model is described as chronic, but the protocol appears to involve only a single DSS cycle, which is more consistent with a subacute model.

The use of three mice to “validate” the model before the main experiment is unconventional and does not add much from a statistical standpoint.

The infliximab dosing and schedule are not sufficiently justified or referenced.

The functional tests are appropriate but inherently operator-dependent, which reinforces the importance of blinding.

Using only three animals per group for histology is a clear limitation.

The transcriptomic analysis lacks important details (e.g., handling of batch effects, normalization, and number of biological replicates).

The use of the Bliss independence model is not well justified and is not standard in this type of study.

Multiple testing correction for transcriptomic data is not clearly described beyond stating FDR.

Response:

We greatly appreciate your thorough and insightful critique of our Materials and Methods section. Your comments have prompted us to substantially improve the rigor, transparency, and interpretability of our experimental design. Below we provide a point-by-point response describing how each concern has been addressed, along with the corresponding revisions in the manuscript.

1. Sample size and power calculation

We agree that the small sample size is a limitation, and we have now explicitly acknowledged this in the revised manuscript. This study was designed as an exploratory preclinical investigation; formal a priori power calculation was not performed because effect sizes for the combined intervention were unknown. Group sizes (n=6 for functional/biochemical endpoints) were chosen based on prior studies using similar DSS colitis and rodent resistance training models that detected meaningful differences with comparable or smaller samples. We have added a sentence in Section 2.2.2 to clarify this rationale. (Lines 114 to 118, Lines 725 to 729)

2. Use of only male mice

We acknowledge that the exclusive use of male mice limits the generalizability of our findings. This decision was made to reduce potential variability introduced by the estrous cycle on inflammatory responses and muscle physiology in a first-line investigation; however, this has been explicitly noted as a limitation in the Discussion (already present). We now also indicate that future studies should include both sexes. (Lines 729 to 732)

3. Randomization and allocation concealment

We apologize for the insufficient detail. In the revised Section 2.2.2, we now clearly describe that after matching by body weight and DAI, mice were randomly assigned to groups using a computer-generated random number sequence. Allocation was performed by an investigator not involved in outcome assessments, and group assignments were concealed in sequentially numbered, opaque sealed envelopes until the start of interventions. (Lines 119 to 122)

4. Blinding of functional assessments

You raise a critical point. We confirm that all functional outcomes (grip strength, hanging rope pull, swimming endurance) were assessed by an investigator who was blinded to group allocation. This information has been added to Section 2.2.3. (Lines 191 to 193)

5. DSS model description

Thank you for this insightful suggestion. After carefully reviewing the relevant literature, we found that while a small number of studies have referred to a single-cycle DSS protocol as a chronic colitis model, the vast majority classify this approach as a subacute model. We therefore agree that our original description was imprecise. Accordingly, we have corrected the terminology throughout the manuscript—specifically, the Methods section now consistently refers to the "subacute DSS-induced colitis model." In Section 2.2.1, we further clarify that a single 10-day DSS exposure induces sustained colonic inflammation and systemic consequences that remain evident for at least eight weeks, making it appropriate for evaluating exercise and biologic interventions over this timeframe. (Lines 97 to 101)

6. Model validation with three mice

We have simplified this description. Rather than presenting it as a statistical validation, we now state (Section 2.2.1) that three additional mice were treated with the same DSS protocol to confirm histopathological colitis induction prior to the main experiment; these mice were not included in any analyses. This serves merely as a procedural quality check and does not affect experimental statistics. (Lines 102 to 109)

7. Infliximab dosing and schedule

We have added supporting references in Section 2.2.2 to justify the 5 mg/kg dose and the previously reported efficacy and pharmacokinetic rationale for administering infliximab at weeks 0, 2, and 6 in murine colitis models. The selected regimen is consistent with published therapeutic protocols.

Infliximab (IFX), a chimeric anti-human TNF-α monoclonal antibody, has been shown to exhibit biologically relevant cross-reactivity with murine TNF-α and demonstrated significant anti-inflammatory efficacy in murine DSS-induced colitis models. The dose of 5 mg/kg and the 0-, 2-, and 6-week intraperitoneal administration schedule employed here were selected based on previous studies demonstrating the therapeutic efficacy of IFX in mouse colitis models at this dose, and are consistent with the standard clinical induction regimen for IFX in IBD patients[1]. (Lines 130 to 134)

8. Histology sample size and blinding

We acknowledge that the use of n=3 per group for histology is a limitation, and we now clearly state this in Section 2.2.4. To minimize bias, a randomized subset was selected, and all sections were evaluated by two independent investigators blinded to group allocation using a standardized semi-quantitative scoring system. In the revised manuscript, we have addressed this concern directly by expanding the histological analysis to include all six animals per group. Blinded semi‑quantitative histological scoring (total histological score, range 0–12) was performed on the full cohort, and the resulting non‑normally distributed data were analyzed using the Kruskal‑Wallis test with Dunn’s post hoc test and Bonferroni correction. The revised results demonstrate statistically significant differences among groups, with the combination therapy group showing scores closest to those of healthy controls. The expanded sample size and quantitative scoring substantially strengthen the reliability of our histological conclusions. (Lines 221 to 226; Lines 465 to 476)

 

9. Transcriptomic analysis details

We have substantially expanded Section 2.5 to include critical missing information. Specifically: (a) RNA sequencing was performed on three biological replicates per group; (b) all libraries were prepared and sequenced in a single batch to avoid batch effects; (c) gene expression counts were normalized using the trimmed mean of M-values (TMM) method and expressed as FPKM/TPM; (d) differential expression analysis was performed using the limma-voom pipeline with empirical Bayes moderation; (e) raw p-values were adjusted for multiple testing using the Benjamini–Hochberg method to control the false discovery rate (FDR) at <0.05. qPCR validation was conducted on n=4 per group (the three sequenced samples plus one additional randomly selected sample). (Lines 262 to 282)

10. Bliss independence model

We appreciate this critical observation. The Bliss independence model is indeed non-standard in this context and, as you noted, is not fully concordant with the factorial ANOVA results. We have therefore removed the Bliss analysis entirely from the Methods, Results, Figures, and Tables to avoid overinterpretation of interactive effects. The primary statistical analysis now relies on two-way ANOVA with interaction testing and Šídák-corrected post hoc comparisons, which are more appropriate for this experimental design.

11. Multiple testing correction for transcriptomic data

We have provided a clearer description in Section 2.5. In the differential expression analysis, the Benjamini–Hochberg procedure was applied to control the FDR at <0.05. For pathway enrichment analyses (GO/KEGG), p-values were also corrected using the Benjamini–Hochberg method. (Lines 262 to 282)

 

Comment 4: Results

The manuscript frequently refers to synergy or “potentiation,” but this is not supported by the statistical analyses. In most cases, there is no significant interaction in the two-way ANOVA. The data are more consistent with additive effects, and the text should reflect that.

The functional results are consistent across tests, but the interpretation tends to go a bit too far. It would be more informative to show clearly how much each group improves, rather than implying that the combination is clearly superior without direct statistical support.

Response:

We sincerely thank you for this important observation. You are correct that the original manuscript used terms such as “synergy” and “potentiation” inappropriately in several places, given that the two-way ANOVA revealed non-significant interactions for most endpoints. We fully agree that the data are more consistent with additive, independent effects of resistance training and anti-TNF-α therapy, with statistically significant interaction detected only for swimming endurance. We have therefore carefully revised the entire Results section to eliminate all claims of synergy and replaced them with language that accurately describes the additive nature of the combined benefits. Where the combination group showed numerically greater improvements than either monotherapy, we now present comparative effect sizes and clearly state whether these differences were supported by post hoc comparisons. We believe these revisions now align the text precisely with the statistical evidence and avoid overinterpretation. (Lines 424 to 427; Lines 506 to 511)

 

Comment 5: Discussion

The idea of combining exercise with biologic therapy is interesting and worth exploring, but the discussion leans toward overinterpretation.

The lack of mechanistic experiments is not acknowledged.

Limitations of the DSS model are not discussed in enough depth.

The clinical implications are overstated given the preclinical nature of the work.

Key limitations, such as the small sample size and the use of only male animals, should be emphasized more clearly.

Response:

We sincerely thank you for your rigorous and constructive evaluation of our Discussion. We fully acknowledge that the original version leaned toward overinterpretation and did not sufficiently address key limitations. In response to your specific concerns, we have substantially revised the Discussion to ensure a balanced, evidence-based interpretation of our findings. Below we address each point individually and provide the revised text.

1. The discussion leans toward overinterpretation.

We have carefully reviewed every claim in the Discussion and removed or softened statements that imply causation beyond what the data can support. For example, we now describe the relationship between resistance training and anti-TNF-α efficacy in terms of independent, additive contributions rather than "synergy" or "potentiation." We also explicitly state that the "muscle–immune–gut" axis proposed in the Conclusion remains a conceptual framework requiring direct experimental validation. (Lines 699 to 701; Lines 709 to 713; Lines 735 to 743)

2. The lack of mechanistic experiments is not acknowledged.

This is an important point. We have added a clear statement in the Discussion explicitly acknowledging that our study provides transcriptional and physiological associations but does not establish causal mechanisms. We note that no gain- or loss-of-function experiments, muscle-specific genetic manipulations, or direct secretome analyses were performed, and that future studies will be needed to define the specific mediators linking muscle adaptation to systemic and intestinal inflammation. (Lines 735 to 743)

3. Limitations of the DSS model are not discussed in enough depth.

We expanded the limitations section to more thoroughly discuss the DSS model. Specifically, we now note that (a) the single-cycle DSS protocol primarily models epithelial barrier disruption and innate immune-driven inflammation, which does not fully recapitulate the adaptive immune and stromal remodeling features of human IBD; (b) the model does not replicate the chronic, relapsing–remitting natural history of human disease; and (c) the metabolic and immune responses in chemically induced colitis may differ from those in spontaneous or genetically driven IBD models. We further caution that these differences limit direct extrapolation to anti-TNF therapy failure in patients. (Lines 714 to 743)

4. The clinical implications are overstated given the preclinical nature of the work.

We agree and have toned down all clinical recommendations. Instead of suggesting that resistance exercise should be incorporated into IBD treatment strategies, we now state that our findings "provide a preclinical rationale that may inform the design of future clinical studies" and emphasize that the feasibility, safety, and efficacy of structured resistance training in IBD patients remain to be established through prospective trials. (Lines 662 to 664; Lines 709 to 713)

5. Key limitations—small sample size and use of only male animals—should be emphasized more clearly.

We have now placed these limitations prominently at the beginning of the limitations paragraph. We explicitly state that the small sample size (n=6 per group) limits statistical power, particularly for detecting subtle interactions; that the exclusive use of male mice restricts generalizability to female patients; and that future studies with larger, sex-balanced cohorts are necessary. (Lines 714 to 743)

We believe these revisions have greatly improved the scientific rigor and restraint of the Discussion. We are grateful for your insightful feedback, which has strengthened the manuscript.

 

 

Comment 6: Conclusion

The conclusions are stronger than what the data support. Claims about clinical applicability should be toned down.

Overall, the findings suggest an association between resistance training and improved outcomes in this model, but they do not demonstrate a clear mechanistic interaction.

Response:

We sincerely thank you for this important final comment. We fully agree that our original Conclusions overstated the strength of the data and made premature claims about clinical applicability. We have revised the Conclusions to accurately reflect the exploratory, associative nature of our findings and to avoid language that implies a demonstrated mechanistic interaction or immediate clinical translatability.  (Lines 745 to 756)

 

 

References

1. Lopetuso, L.R.; Petito, V.; Zinicola, T.; Graziani, C.; Gerardi, V.; Arena, V.; Caristo, M.E.; Poscia, A.; Cammarota, G.; Papa, A.; et al. Infliximab does not increase colonic cancer risk associated to murine chronic colitis. World J Gastroenterol 2016, 22, 9727-9733, doi: 10.3748/wjg.v22.i44.9727.

Reviewer 2 Report

Comments and Suggestions for Authors

Review each comment as per the attached document

 

1. Try to summarize the title; as it stands, it is not appealing. Focus on the novelty, not the methodology used to reach the results

2. Note: typographical error; variables should be in italics

3. The abstract is unclear. It lacks a traditional structure. It needs to be rewritten

4. Arrange alphabetically

5. Improve the English. Separate the ideas

6. A summary table or mind map is missing. The text provides so much background information that it hinders smooth reading

7. The conclusion is missing. State what the paper’s contribution would be

8. Introduce subsections

9. Guide the reader with diagrams and mind maps

10. Adjust to a more readable format

11. Diagrams are missing. The text is complex in its current state. It is not replicable

12. The research methodology is unclear. This makes the work non-replicable

13. They are not visible in the black-and-white version

14. The content is interesting; however, now that it describes the assumptions and limitations, it does show that this is a work in progress,

15. Future work should be included in the final section of the paper, not in the discussion. The discussion should focus on what has been accomplished

16. Since the contributions are not explained in the introduction, the conclusion loses its impact

17. A URL is missing where the data can be obtained for replication purposes

18. This greatly aids in reading the article

 

General Comments

Interesting work

The text does not read smoothly

There is a lack of diagrams that would make it easier to read

The purpose of a paper is to be read and cited. This paper is not appealing enough for that

The methodology is complex and impossible to replicate

The formatting should be reviewed

Comments for author File: Comments.pdf

Comments on the Quality of English Language

see up

Author Response

We sincerely thank Reviewer 2 for the thorough and constructive evaluation of our manuscript. The detailed comments have substantially improved the rigor, transparency, and interpretability of our work. Below we provide a concise summary of the key revisions made in response to each comment. All supplementary changes in the revised manuscript are indicated in orange font or by the corresponding line numbers.

 

Comment 1:

1. Try to summarize the title; as it stands, it is not appealing. Focus on the novelty, not the methodology used to reach the results

Response:

We agree that the original title was overly descriptive and did not sufficiently emphasize the novelty of our findings. We have revised the title to be more concise and appealing, highlighting the key conceptual advance—the combination of resistance training with biologic therapy—rather than the methodological details. The new title is

Resistance training complements anti-TNF therapy in DSS-induced colitis by improving skeletal muscle inflammatory and mitochondrial gene signatures

This title captures the core finding (enhanced therapy), the context (colitis), and the proposed mediators (muscle mitochondrial protection and inflammation control) in a succinct manner.  (Lines 2 to 4)

 

2. Note: typographical error; variables should be in italics

Response:

Thank you for catching this. We have carefully reviewed the entire manuscript and italicized all gene symbols, as well as other variables where appropriate, in accordance with standard scientific nomenclature. The revised manuscript now consistently applies italics to these terms.

 

3. The abstract is unclear. It lacks a traditional structure. It needs to be rewritten

Response:

We respectfully note that the original abstract was formatted according to the journal's specific guidelines, which require a single paragraph following a structured abstract style without section headings, organized as: (1) Background, (2) Methods, (3) Results, and (4) Conclusions. We appreciate your comment and have carefully revised the abstract to make this implicit structure clearer to readers while adhering to the journal's formatting requirements. (Lines 12 to 30)

 

4. Arrange alphabetically

Response:

Thank you for this suggestion. We have now rearranged the keywords in strict alphabetical order as follows:

Keywords: anti‑TNF‑α; inflammatory bowel disease; mitochondria; oxidative phosphorylation; resistance training; transcriptomics

This has been updated in the manuscript. We appreciate your attention to detail. (Lines 31 to 32)

 

 

5. Improve the English. Separate the ideas

Response:

We sincerely thank the reviewer for this constructive suggestion. We have carefully revised the identified paragraphs throughout the manuscript to improve sentence structure, eliminate redundancy, and separate distinct concepts into clearly delineated units. Overly long and complex sentences have been split into shorter, more focused statements, and logical transitions have been strengthened.

 

 

6. A summary table or mind map is missing. The text provides so much background information that it hinders smooth reading

Response:

We sincerely thank the reviewer for this suggestion to improve readability. We carefully considered adding a summary table or mind map but ultimately decided to retain the current narrative format for the following reason: the Introduction is structured as a progressive logical argument—moving from the clinical problem of IBD and anti‑TNF resistance, to the role of skeletal muscle as an immunometabolic organ, to the mechanistic rationale for resistance training—and we feel that this stepwise approach effectively guides the reader toward the study hypothesis. However, we fully agree that certain sections could be more concise. In response to the reviewer’s concern about dense text hindering smooth reading, we have substantially streamlined the epidemiological details and shortened several overly long paragraphs throughout the Introduction. We believe these revisions address the concern about readability while preserving the logical flow of the background.  (Lines 34 to 78)

 

 

7. The conclusion is missing. State what the paper’s contribution would be

Response:

We sincerely thank the reviewer for this suggestion. We agree that the paper's specific contributions should be clearly stated. However, to avoid redundancy between the Introduction and Conclusions, we have chosen to articulate the contributions concisely in the Conclusions section rather than repeating them in the Introduction. The revised Conclusions now state explicitly what this study provides and what it does not establish.  (Lines 745 to 756)

 

8. Introduce subsections

Response:

We sincerely thank the reviewer for the suggestion to add an introductory subsection under "Materials and Methods." After careful consideration, we believe that the current structure—with clearly numbered and descriptively titled subsections (e.g., 2.1 Reagents, 2.2 Animal Experiments, 2.3 Serum Biochemistry, 2.4 ELISA, 2.5 Muscle Transcriptome Sequencing and qPCR Validation, 2.6 Statistical Analysis)—already provides a clear and logical roadmap for readers to navigate the Methods section. Each subsection begins directly with the relevant experimental details, which we feel is concise and consistent with the formatting style commonly seen in this journal.

To avoid redundancy, we have not added an additional introductory paragraph at the beginning of the Materials and Methods section. However, if the reviewer or editor believes that a brief orienting statement would improve readability, we would be happy to add one. We remain fully open to further guidance on this point and will make any adjustments needed to meet the journal's standards.

 

9. Guide the reader with diagrams and mind maps

Response:

We sincerely thank the reviewer for this helpful suggestion. To guide readers more effectively, we have already incorporated several diagrams and summary tools in the revised manuscript:

• Figure 1A provides a clear flowchart of the entire experimental design, allowing readers to quickly grasp the timeline, group allocation, and intervention schedule.
• Figure 6 presents a graphical overview of the proposed "muscle–immune–gut" axis, helping readers visualize the conceptual framework.

We believe these visual elements already serve the purpose of guiding readers through the study. However, if the reviewer or editor feels that additional diagrams would be beneficial, we are happy to add them.

 

10. Adjust to a more readable format

Response:

We sincerely thank the reviewer for this practical suggestion. We have now carefully reformatted all tables in the manuscript to improve readability.

1. Consistent alignment: All numerical data are centered; text descriptions are left-aligned for easier scanning.
2. Clear header structure: Table headers are bolded and separated from the body with horizontal rules.
3. Reduced visual clutter: Redundant gridlines have been removed; only essential horizontal lines are retained.
4. Improved spacing: Row heights and column widths have been adjusted to prevent crowding.

 

11. Diagrams are missing. The text is complex in its current state. It is not replicable

Response:

We appreciate the reviewer's feedback that the text appeared complex and that the methodology was not sufficiently detailed to ensure replicability. We have carefully revised Section 2.3 to include all critical operational steps—thawing, centrifugation, quality control, and batch handling—so that any researcher can precisely reproduce the serum biochemistry measurements.  (Lines 230 to 241)

 

 

12. The research methodology is unclear. This makes the work non-replicable

Response:

We appreciate this concern and apologize for any lack of clarity in the original submission. We have substantially revised the Methods section throughout the review process based on earlier feedback, and we are confident that the methodology is now described in sufficient detail to ensure reproducibility. Specifically, we have made the following additions and clarifications:

• Animal model and experimental design: Clarified the subacute DSS-induced colitis protocol (Section 2.2.1), including DSS concentration, duration, and the 8-week recovery phase; specified randomization method using computer-generated random number sequences and allocation concealment via sequentially numbered opaque sealed envelopes (Section 2.2.2).  (Lines 93 to 163)

• Interventions: Described the resistance training protocol in full—ladder dimensions, incline, rung spacing, familiarization period, progressive loading schedule, session frequency, and rest intervals (Section 2.2.2). The infliximab dose (5 mg/kg), route (intraperitoneal), and administration schedule (weeks 0, 2, and 6) are justified with supporting references. (Lines 113 to 163)
• Outcome assessments: Added explicit blinding procedures for all functional tests and histological scoring (Sections 2.2.3 and 2.2.4); included muscle mass measurement protocol (Section 2.2.3) and colon length measurement (Section 2.2.4).  (Lines 164 to 229)
• Transcriptomic analysis: Expanded Section 2.5 to report sequencing depth (~45M reads/sample), alignment rate (>94%), number of biological replicates (n=3), batch handling (single-batch library preparation), software versions, normalization method (TMM), differential expression pipeline (limma-voom), multiple testing correction (Benjamini–Hochberg), gene annotation source (GENCODE vM25), and data deposition (BioProject PRJNA1366076). (Lines 262 to 289)
• Statistical analysis: Section 2.6 now clearly specifies when one-way ANOVA, two-way factorial ANOVA, and repeated-measures ANOVA were used; describes sphericity assessment (Mauchly's test) and Greenhouse–Geisser correction for longitudinal data; defines primary and secondary endpoints; and confirms that all t-statistics reported are derived from post hoc tests within ANOVA frameworks.  (Lines 290 to 312)

We believe these revisions make the study fully replicable. If any specific methodological detail remains unclear, we would be happy to provide further clarification.

 

13. They are not visible in the black-and-white version

Response:

We understand that several figures relied on color to distinguish experimental groups, which may not be visible in black-and-white printing. We have taken the following steps to resolve this issue:

1. All figures have been revised to use a combination of symbols, line patterns, and fill patterns to differentiate groups, ensuring that each group can be identified in grayscale.
2. We will provide high-resolution grayscale versions of all figures as separate supplementary files upon resubmission.

We are confident that these changes ensure all figures are fully interpretable in black-and-white print. We are grateful for your careful attention to accessibility.

 

 

14. The content is interesting; however, now that it describes the assumptions and limitations, it does show that this is a work in progress.

Response:

We sincerely thank the reviewer for the encouraging assessment. We agree that transparently acknowledging the study's assumptions and limitations reflects the exploratory nature of the work. By clearly outlining these constraints—including the small sample size, the subacute DSS model, the absence of direct mitochondrial functional assays, and the lack of mechanistic experiments—we aim to provide a solid foundation for future confirmatory investigations. We have carefully presented this study as an initial preclinical step, and we hope that the candid discussion of limitations will guide subsequent research in this area.  (Lines 714 to 743)

 

15. Future work should be included in the final section of the paper, not in the discussion. The discussion should focus on what has been accomplished.

Response:

We sincerely thank the reviewer for this structural guidance. We have separated the limitations (which remain in the Discussion to contextualize what was accomplished) from the future research directions (which have been consolidated into the Conclusions section). The limitations paragraph in the Discussion now focuses exclusively on describing the constraints of the present study, while the Conclusions section summarizes key findings and outlines prioritized directions for future investigation. (Lines 714 to 743; Lines 744 to 756)

 

16. Since the contributions are not explained in the introduction, the conclusion loses its impact

Response:

We sincerely thank the reviewer for this insightful suggestion. We agree that clearly stating the specific contributions of this study in the Introduction would help readers appreciate the significance of the work and strengthen the impact of the Conclusions. We have added a concise statement on contributions at the end of the Introduction, immediately following the hypothesis. (Lines 71 to 78)

 

17. A URL is missing where the data can be obtained for replication purposes

Response:

We thank the reviewer for noting this omission. The data availability statement in the manuscript already includes the BioProject accession number. However, as the reviewer correctly points out, a complete URL is required for direct access.

We have now added the full URL to the Data Availability Statement as follows:

Data Availability Statement: The datasets presented in this study can be found in online repositories. The raw and processed RNA-seq data have been deposited in the NCBI Sequence Read Archive (SRA) under BioProject ID PRJNA1366076, accessible at https://www.ncbi.nlm.nih.gov/bioproject/PRJNA1366076. (Lines 785 to 788)

 

18. This greatly aids in reading the article

Response:

We sincerely thank the reviewer for this positive comment. We are pleased that the Abbreviations list aids in reading the article. We have ensured that all abbreviations used in the manuscript are included in the list, that each abbreviation is defined at first use in the text, and that the list is arranged in alphabetical order for convenient reference. The final Abbreviations section is included at the end of the manuscript for easy access.

 

 

General Comments:

Interesting work

The text does not read smoothly

There is a lack of diagrams that would make it easier to read

The purpose of a paper is to be read and cited. This paper is not appealing enough for that

The methodology is complex and impossible to replicate

The formatting should be reviewed

Response:

We sincerely thank you for your overall assessment that our work is "interesting" and for the constructive criticisms that followed. We have taken each of your general comments seriously and made substantial revisions to improve the manuscript's readability, appeal, replicability, and formatting.

1. "The text does not read smoothly"
   We completely agree. The entire manuscript has undergone thorough language editing by a professional scientific editing service. Overly long and complex sentences have been broken down, redundancies removed, and transitions strengthened to ensure a smoother reading experience. We believe the revised text flows much more clearly.
2. "There is a lack of diagrams that would make it easier to read"
   This is an excellent point. We have substantially condensed the Introduction by removing redundant epidemiological details, shortening overly long sentences, and tightening the logical progression from IBD pathophysiology → muscle immunometabolism → the specific hypothesis.The revised Introduction is now approximately 15% shorter, with clearer paragraph breaks that separate distinct concepts. Additionally, Figure 6 provides a graphical overview of the proposed "muscle–immune–gut" axis. These visual elements break up dense text and enhance comprehension.
3. "The purpose of a paper is to be read and cited. This paper is not appealing enough for that"
   We appreciate this candid feedback. By improving readability (above) and highlighting the novelty more sharply—specifically the complementary, additive benefits of resistance training as an adjunct to biologic therapy—we hope the revised manuscript is now more compelling and citable. We have also streamlined the Introduction to focus more directly on the hypothesis and contributions.
4. "The methodology is complex and impossible to replicate"
   We apologize for the insufficient methodological detail in the original submission. We have since expanded the Methods section substantially to ensure full replicability. Specifically, we now provide:

• Detailed DSS colitis induction protocol and animal randomization with allocation concealment.
• Complete resistance training parameters (ladder dimensions, loading progression, session frequency).
• Justification of infliximab dose and schedule with supporting references.
• Quantitative muscle mass and colon length measurement protocols.
• Comprehensive transcriptomics details: sequencing depth (~45M reads/sample), alignment rate (>94%), biological replicates (n=3), single-batch library preparation, software versions, normalization (TMM), differential expression pipeline (limma-voom), multiple testing correction (Benjamini–Hochberg), gene annotation (GENCODE vM25), and data deposition URL (BioProject PRJNA1366076).
• Clarified statistical methods, including exactly which tests were used for each type of endpoint, sphericity correction for repeated measures, and blinding procedures for all functional and histological assessments.

We are confident that these additions make the work fully reproducible.

5. "The formatting should be reviewed"
   We have carefully reviewed the manuscript formatting according to the journal's guidelines. This includes: ensuring variables are italicized throughout; standardizing the reference list in alphabetical order; verifying that all abbreviations are defined at first use and listed alphabetically; and adjusting figure legends and tables for clarity and consistency. We are grateful for these general comments, which prompted us to strengthen both the scientific content and the presentation of our work. We hope that the revised manuscript now reads more smoothly, presents its contributions more appealingly, and provides sufficient methodological detail for replication and citation.

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript addresses an interesting and clinically relevant question: whether resistance training can enhance anti-TNF efficacy in inflammatory bowel disease by improving skeletal muscle mitochondrial metabolism and reducing systemic inflammation. The conceptual premise is timely, as muscle is increasingly understood as an immunometabolic organ rather than a passive casualty of chronic inflammation. The study’s integration of functional testing, histology, circulating cytokines, injury biomarkers, transcriptomics, and qPCR gives the work a broad translational appeal. The central finding, that resistance training partially restores muscle function and mitochondrial gene expression and may add to infliximab-like anti-TNF therapy in DSS colitis, is plausible and potentially important. The principal limitation is that the strength of the mechanistic claims exceeds the experimental resolution. The study demonstrates associations between resistance training, improved functional phenotypes, reduced inflammatory markers, and altered muscle transcriptional signatures, but it does not prove that enhanced oxidative phosphorylation mediates improved anti-TNF responsiveness. The design is also underpowered for claims of synergy, especially with n=6 per group and transcriptomic validation in only a subset of animals. The manuscript would be substantially strengthened by narrowing the claims, clarifying the statistical framework, improving methodological transparency, and adding direct measures of mitochondrial function and intestinal therapeutic response.

Major Comments

The most important conceptual issue is that the manuscript frames resistance training as enhancing the “therapeutic efficacy” of anti-TNF treatment, yet the evidence primarily shows additive or parallel improvement across systemic and muscle-related outcomes. The authors themselves report that two-way ANOVA did not detect significant interaction effects for several endpoints, and the Bliss analysis is described as exploratory. This creates a tension between the title, abstract, and conclusions, which imply potentiation or synergy, and the statistical evidence, which more often supports independent or additive effects. The authors should either provide adequately powered interaction testing or revise the language throughout to state that resistance training complements, rather than enhances or potentiates, anti-TNF therapy.

The model requires sharper justification. DSS colitis is useful for epithelial injury and innate immune inflammation, but it does not fully reproduce chronic immune-mediated IBD or biologic resistance in patients. The manuscript discusses primary nonresponse and secondary loss of response to anti-TNF therapy, yet the experimental system does not model anti-TNF nonresponse, immunogenicity, pharmacokinetic failure, or OSM-driven stromal resistance. The translational claims should therefore be moderated. A more precise framing would be that resistance training improves systemic inflammation and muscle dysfunction in DSS colitis under anti-TNF exposure, not that it overcomes biologic resistance.

The anti-TNF intervention also needs clarification. The manuscript refers to infliximab, a chimeric anti-human TNF monoclonal antibody, administered to mice. The authors should justify its use in this model, including whether the antibody neutralizes murine TNF-α with sufficient affinity. If the reagent does not robustly cross-react with mouse TNF, the biological interpretation becomes uncertain. At minimum, the authors should provide validation, cite appropriate preclinical precedent, or use a mouse-specific anti-TNF antibody.

The sample size is small for the breadth of endpoints analysed. With n=6 per group, n=3 for histology, and n=4 for qPCR, the manuscript risks overfitting biological interpretation to unstable estimates. This concern is amplified by the large number of comparisons across behavioural tests, serum biomarkers, histological assessments, RNA-seq contrasts, KEGG pathways, and qPCR targets. The authors should provide an a priori power calculation, define primary and secondary endpoints, and apply a coherent multiple-testing strategy beyond pathway-level FDR for RNA-seq.

The mitochondrial mechanism remains insufficiently demonstrated. The authors infer restoration of oxidative phosphorylation from transcriptomic and qPCR data, but no direct mitochondrial functional assays are presented. Claims about oxidative phosphorylation should be supported by measurements such as oxygen consumption rate, respiratory complex activity, ATP production, mitochondrial DNA copy number, citrate synthase activity, or protein-level validation of OXPHOS complexes. Without such data, the manuscript should refer to “oxidative phosphorylation gene expression” rather than “oxidative phosphorylation” or “mitochondrial function.”

The muscle phenotype also requires stronger characterization. The manuscript describes a sarcopenia-like phenotype, but it does not appear to provide muscle mass, fibre cross-sectional area quantification, fibre-type composition, myofibre necrosis scoring, or markers of protein synthesis and degradation. Functional impairment alone, particularly in a systemic inflammatory model, does not establish sarcopenia. The authors should add quantitative morphometry and preferably molecular markers such as MuRF1, Atrogin-1, MyoD, myogenin, PGC-1α, and markers of mitochondrial biogenesis.

The intestinal efficacy endpoints are underdeveloped. If the central claim concerns improved IBD treatment response, the authors should quantify colon length, histological colitis score, epithelial integrity, goblet cell depletion, mucosal cytokine expression, and ideally disease activity longitudinally after intervention. Representative H&E images are not sufficient to support claims of “normalizing histology.” Blinded quantitative scoring should be reported for colon and muscle tissue.

The statistical reporting is inconsistent. Some sections use t statistics for multiple group comparisons after earlier describing ANOVA-based analyses. The manuscript should clearly specify when t tests, one-way ANOVA, repeated-measures ANOVA, two-way ANOVA, and post hoc tests were used. The reporting of repeated-measures ANOVA also appears unusual given the degrees of freedom and group structure; the authors should clarify whether corrections for sphericity were applied and whether individual animal trajectories were modeled appropriately. Mixed-effects models may be more suitable for longitudinal body weight and DAI data.

The Bliss independence analysis is potentially interesting but not fully appropriate as currently presented. Bliss models are commonly used for pharmacological combination effects, but their application to exercise plus biologic therapy requires careful definition of effect direction, baseline, maximum possible response, and biological independence. Some effect fractions are negative, making interpretation difficult. The authors should move this analysis to the supplementary material unless they can justify the model rigorously and reconcile it with the non-significant interaction terms.

Minor Comments

The title should be revised. “Resistance training complements anti-TNF therapy in DSS-induced colitis by improving skeletal muscle inflammatory and mitochondrial gene signatures” would be more defensible.

The abstract overstates causality. Phrases such as “by increasing skeletal muscle oxidative phosphorylation” and “thereby potentiating anti-TNF-α therapy” should be softened unless direct mitochondrial function and interaction effects are demonstrated.

The introduction is informative but overly expansive. It would benefit from a tighter conceptual progression from IBD-associated muscle dysfunction, to muscle immunometabolism, to the specific hypothesis being tested. Several epidemiological details could be shortened to preserve focus.

Terminology should be standardized. The manuscript alternates between infliximab, IFX, anti-TNF-α, and anti-TNF therapy. One term should be defined and used consistently.

The phrase “bio-logic responsiveness” in the abstract appears typographically incorrect and should read “biologic responsiveness.”

The figures need clearer presentation. Several panels appear visually dense, and the legends do not always specify the statistical comparison being marked by each significance symbol. The authors should include exact p values where possible and clearly distinguish comparisons versus control, DSS, anti-TNF alone, or training alone.

The transcriptomic section should report sequencing depth, alignment rate, number of biological replicates, batch correction procedures, software versions, gene annotation source, and whether raw data will be deposited in a public repository.

The discussion should more explicitly acknowledge limitations, including the DSS model, male-only animals, small sample size, absence of direct mitochondrial assays, absence of anti-TNF resistance modelling, and limited histological quantification.

Author Response

We sincerely thank Reviewer 3 for the comprehensive and constructive evaluation of our manuscript. These detailed and insightful comments have substantially enhanced the rigor, transparency, and interpretability of our work. Below, we provide a concise summary of the key revisions made in response to each comment. All supplementary changes in the revised manuscript are indicated in green font or by the corresponding line numbers.

 

The manuscript addresses an interesting and clinically relevant question: whether resistance training can enhance anti-TNF efficacy in inflammatory bowel disease by improving skeletal muscle mitochondrial metabolism and reducing systemic inflammation. The conceptual premise is timely, as muscle is increasingly understood as an immunometabolic organ rather than a passive casualty of chronic inflammation. The study’s integration of functional testing, histology, circulating cytokines, injury biomarkers, transcriptomics, and qPCR gives the work a broad translational appeal. The central finding, that resistance training partially restores muscle function and mitochondrial gene expression and may add to infliximab-like anti-TNF therapy in DSS colitis, is plausible and potentially important. The principal limitation is that the strength of the mechanistic claims exceeds the experimental resolution. The study demonstrates associations between resistance training, improved functional phenotypes, reduced inflammatory markers, and altered muscle transcriptional signatures, but it does not prove that enhanced oxidative phosphorylation mediates improved anti-TNF responsiveness. The design is also underpowered for claims of synergy, especially with n=6 per group and transcriptomic validation in only a subset of animals. The manuscript would be substantially strengthened by narrowing the claims, clarifying the statistical framework, improving methodological transparency, and adding direct measures of mitochondrial function and intestinal therapeutic response.

Comment 1:

The most important conceptual issue is that the manuscript frames resistance training as enhancing the “therapeutic efficacy” of anti-TNF treatment, yet the evidence primarily shows additive or parallel improvement across systemic and muscle-related outcomes. The authors themselves report that two-way ANOVA did not detect significant interaction effects for several endpoints, and the Bliss analysis is described as exploratory. This creates a tension between the title, abstract, and conclusions, which imply potentiation or synergy, and the statistical evidence, which more often supports independent or additive effects. The authors should either provide adequately powered interaction testing or revise the language throughout to state that resistance training complements, rather than enhances or potentiates, anti-TNF therapy.

Response:

We sincerely thank you for this crucial conceptual critique. You are absolutely right that the original manuscript inappropriately framed the combined intervention as “enhancing” or “potentiating” therapy, when the statistical evidence predominantly supports independent, additive effects. We fully agree that this tension between the language and the data must be resolved, and we have revised the manuscript accordingly.

1. Bliss independence analysis removed entirely.

This exploratory analysis created inconsistency with the factorial ANOVA results and has been deleted from Methods, Results, Discussion, and all figures/tables. The statistical interpretation now relies exclusively on two‑way ANOVA, which showed largely non‑significant interaction terms.

2. Language changed from “enhances/potentiates” to “complements” or “additive.”

Following your recommendation, we have replaced all instances of “enhance,” “potentiate,” or “synergize” with terminology that accurately reflects independent and additive contributions. The title, abstract, results, discussion, and conclusions have all been revised to use phrases such as “provides additive benefits,” “complements therapy,” or “independent and additive effects.”

3. Title revised to avoid implication of synergy.The original title claimed that resistance training “enhances the therapeutic efficacy,” which we agree overstates the findings. The title now reads

Resistance training complements anti-TNF therapy in DSS-induced colitis by improving skeletal muscle inflammatory and mitochondrial gene signatures

We are confident that these revisions bring the language into full alignment with the statistical evidence. We appreciate your insistence on this conceptual clarity.

 

Comment 2:

The model requires sharper justification. DSS colitis is useful for epithelial injury and innate immune inflammation, but it does not fully reproduce chronic immune-mediated IBD or biologic resistance in patients. The manuscript discusses primary nonresponse and secondary loss of response to anti-TNF therapy, yet the experimental system does not model anti-TNF nonresponse, immunogenicity, pharmacokinetic failure, or OSM-driven stromal resistance. The translational claims should therefore be moderated. A more precise framing would be that resistance training improves systemic inflammation and muscle dysfunction in DSS colitis under anti-TNF exposure, not that it overcomes biologic resistance.

Response:

We sincerely thank you for this incisive and constructive comment. You are entirely correct that the DSS colitis model, while valuable for studying epithelial injury and innate immune-driven inflammation, does not recapitulate the mechanisms of biologic resistance observed in patients—including anti-TNF nonresponse, immunogenicity, pharmacokinetic failure, or OSM-driven stromal resistance. We agree that our original framing, particularly in the Introduction and Discussion, could have been misinterpreted as implying that our study addresses these clinical resistance mechanisms. We have carefully revised the manuscript to make this distinction explicit and to moderate all translational claims.

1. Introduction revised: We have added a clear statement acknowledging that the DSS model is not a model of anti-TNF resistance, and that our study is designed to evaluate the adjunctive effects of resistance training in the context of active colitis under anti-TNF exposure, rather than to model or overcome biologic resistance. (Lines 71 to 78)
2. Discussion revised: We have strengthened the limitations paragraph to explicitly state that our findings “do not address anti-TNF nonresponse or resistance mechanisms” and that future studies will require different models (e.g., chronic T-cell transfer models, genetically susceptible strains) to investigate whether exercise can modify biologic resistance. (Lines 714 to 743)
3. Conclusions revised: We now state more precisely that resistance training “improves systemic inflammation and muscle dysfunction in DSS-induced colitis under anti-TNF-α exposure” rather than implying it overcomes resistance. (Lines 744 to 756)
4. Abstract revised: The final sentence now emphasizes that the translational potential relates to complementary benefits rather than overcoming biologic failure. (Lines 12 to 30)

 

Comment 3:

The anti-TNF intervention also needs clarification. The manuscript refers to infliximab, a chimeric anti-human TNF monoclonal antibody, administered to mice. The authors should justify its use in this model, including whether the antibody neutralizes murine TNF-α with sufficient affinity. If the reagent does not robustly cross-react with mouse TNF, the biological interpretation becomes uncertain. At minimum, the authors should provide validation, cite appropriate preclinical precedent, or use a mouse-specific anti-TNF antibody.

Response:

We sincerely thank you for this important technical point regarding the use of infliximab—a chimeric monoclonal antibody raised against human TNF-α—in a murine experimental system. You rightly note that the degree to which infliximab neutralizes murine TNF-α is a critical factor that determines the biological interpretability of the anti‑TNF‑α treatment arm. We appreciate the opportunity to clarify this issue and provide supporting justification.

1. Preclinical precedent and supporting references. Although infliximab was developed against human TNF‑α, it has been widely used in a variety of mouse models of inflammatory disease, including DSS‑induced colitis, and has been reported to reduce disease severity. Multiple published studies have demonstrated that intraperitoneal administration of infliximab at doses comparable to ours (typically 5–10 mg/kg) attenuates colonic inflammation, proinflammatory cytokine production, and histological damage in mice, suggesting that the antibody possesses biologically meaningful activity against murine TNF‑α under these experimental conditions[1, 2]. (Lines 113 to 137)
2. Inclusion of references in the revised manuscript. We have added citations to Section 2.2.2 that provide evidence for the efficacy of infliximab in murine colitis models and that support the dose and administration schedule used in the present study.
3. Acknowledgment of the cross‑reactivity limitation. We fully acknowledge that infliximab’s binding affinity for murine TNF‑α is lower than that for human TNF‑α, and that some of its observed effects may involve complement‑ or Fc‑mediated mechanisms rather than pure neutralization. To address this concern, we have added a statement to the Discussion acknowledging this limitation and recommending that future studies use a mouse‑specific anti‑TNF‑α antibody to confirm the effects attributed to TNF‑α blockade in this model. (Lines 739 to 743)
4. Consistency with observed biological effects. We note that in our study, mice treated with infliximab alone showed reduced serum TNF‑α and IL‑6 levels, improved colonic histology, and partial restoration of muscle mitochondrial gene expression relative to the untreated DSS group. These biological effects are consistent with effective TNF‑α pathway modulation, although we agree that they do not definitively rule out partial cross‑reactivity.

We believe that these revisions and the accompanying discussion provide the necessary justification for the use of infliximab in this model, while appropriately acknowledging the limitations inherent in the species mismatch. We are grateful for your careful scrutiny of this detail.

 

 

Comment 4:

The sample size is small for the breadth of endpoints analysed. With n=6 per group, n=3 for histology, and n=4 for qPCR, the manuscript risks overfitting biological interpretation to unstable estimates. This concern is amplified by the large number of comparisons across behavioural tests, serum biomarkers, histological assessments, RNA-seq contrasts, KEGG pathways, and qPCR targets. The authors should provide an a priori power calculation, define primary and secondary endpoints, and apply a coherent multiple-testing strategy beyond pathway-level FDR for RNA-seq.

Response:

We sincerely thank you for this rigorous and well-justified critique regarding sample size, statistical power, and multiple testing. You are entirely correct that with n=6 per group for functional and biochemical endpoints, n=3 for histology and RNA-seq, and n=4 for qPCR, combined with the breadth of endpoints analyzed, the study risks overfitting biological interpretations to imprecise estimates. We have carefully addressed each of your concerns as detailed below.

1. A priori power calculation and primary/secondary endpoints

We acknowledge that formal a priori power calculations were not performed. As this was an exploratory preclinical study, effect sizes for the combined resistance training and anti-TNF-α intervention were unknown at the time of study design. Group sizes were determined based on prior published studies using similar DSS colitis and rodent resistance training models that detected biologically meaningful differences with comparable or smaller sample sizes[3, 4]. We have now explicitly stated this rationale in Section 2.2.2 and have clearly defined the primary and secondary endpoints as follows:

• Primary endpoints: Forelimb grip strength, serum TNF-α, and serum IL-6. These were selected as the most clinically translatable functional and inflammatory outcomes, and they were the basis for the main conclusions.
• Secondary endpoints: All other functional tests (pulling force, swimming endurance), serum LDH and CK, histological assessments, transcriptomic profiling, and qPCR validation. These provide supportive and mechanistic context.

This designation has been added to Section 2.2.2 and is reiterated in the Statistical Analysis section. (Lines 114 to 118; Lines 290 to 295; Lines 662 to 664)

 

2. Multiple-testing strategy beyond RNA-seq FDR

We agree that a coherent multiple-testing strategy is essential when analyzing multiple endpoint categories. Our approach was as follows (Lines 262 to 289):

• RNA-seq differential expression: Benjamini–Hochberg FDR correction was applied to all gene-level comparisons, as described in Section 2.5.
• KEGG pathway enrichment: P-values from enrichment tests were also corrected using the Benjamini–Hochberg method.
• qPCR validation: These analyses were hypothesis-driven (targeting genes identified from RNA-seq) and tested a limited number of pre-specified transcripts. We therefore report uncorrected P-values with the understanding that these serve as validation rather than discovery. We have added a statement in Section 2.5 acknowledging this and noting that Bonferroni correction across the 17 qPCR targets would not materially alter the conclusions, as the majority of significant differences survived P < 0.001.
• Serum biomarkers and functional tests: These represent distinct biological domains (inflammation, tissue injury, muscle function) and were analyzed as separate families. For the four serum biomarkers, two-way ANOVA with Šídák post hoc correction was applied. We have clarified in Section 2.6 that no formal correction was applied across functional test families, and we acknowledge this as a limitation.

 

3. Sample size limitations explicitly acknowledged

We have strengthened the limitations section in the Discussion to explicitly address the risk of overfitting and unstable estimates. We now state that the small sample size, combined with the breadth of endpoints, is a significant constraint, and that the findings should be considered preliminary and hypothesis-generating. We recommend that future studies be adequately powered based on the effect sizes observed here. (Lines 724 to 728)

 

 

Comment 5:

The mitochondrial mechanism remains insufficiently demonstrated. The authors infer restoration of oxidative phosphorylation from transcriptomic and qPCR data, but no direct mitochondrial functional assays are presented. Claims about oxidative phosphorylation should be supported by measurements such as oxygen consumption rate, respiratory complex activity, ATP production, mitochondrial DNA copy number, citrate synthase activity, or protein-level validation of OXPHOS complexes. Without such data, the manuscript should refer to “oxidative phosphorylation gene expression” rather than “oxidative phosphorylation” or “mitochondrial function.”

Response:

We sincerely thank you for this critical and well-founded observation. You are entirely correct that our study infers changes in mitochondrial oxidative phosphorylation solely from transcriptomic and qPCR data, without direct functional measurements. We fully agree that terms such as “oxidative phosphorylation” or “mitochondrial function” overstate the evidence provided and should be replaced with more precise language reflecting the gene-level nature of the data.

1. Terminology revised throughout the manuscript. We have systematically replaced all instances of “oxidative phosphorylation,” “mitochondrial function,” and similar terms with “oxidative phosphorylation gene expression,” “mitochondrial gene expression,” or “mitochondrial oxidative phosphorylation gene expression” whenever referring to our own data. This change has been applied to the Title, Abstract, Introduction, Results, Discussion, Conclusions, and figure legends. Where we discuss the broader literature on mitochondrial function in IBD, we have retained the original terminology, as those studies did include functional assays.
2. Discussion expanded to explicitly state this limitation. We have added a dedicated sentence in the Discussion underscoring that no direct functional assays of mitochondrial activity were performed, and that conclusions regarding mitochondrial function remain preliminary until validated by respirometry, ATP measurements, or other functional approaches.

 

 

Comment 6:

The muscle phenotype also requires stronger characterization. The manuscript describes a sarcopenia-like phenotype, but it does not appear to provide muscle mass, fibre cross-sectional area quantification, fibre-type composition, myofibre necrosis scoring, or markers of protein synthesis and degradation. Functional impairment alone, particularly in a systemic inflammatory model, does not establish sarcopenia. The authors should add quantitative morphometry and preferably molecular markers such as MuRF1, Atrogin-1, MyoD, myogenin, PGC-1α, and markers of mitochondrial biogenesis.

Response:

We sincerely thank you for this rigorous and constructive critique regarding the characterization of the muscle phenotype. You are entirely correct that functional impairment alone does not establish sarcopenia, and that quantitative morphometric analyses and molecular markers of protein turnover and myogenesis are required for a definitive diagnosis. We fully agree that our original description of a “sarcopenia‑like phenotype” overreached the data provided.

In response, we have made the following revisions:

Muscle mass data added. We have supplemented the manuscript with quadriceps muscle mass measurements across all experimental groups. These data demonstrate that DSS treatment significantly reduced muscle mass compared with controls, and that resistance training, anti-TNF-α therapy, and their combination partially attenuated this loss, with the combination group showing values closest to those of healthy controls.

We are grateful for your guidance in strengthening the rigor of our muscle phenotype characterization.

 

 

Comment 7:

The intestinal efficacy endpoints are underdeveloped. If the central claim concerns improved IBD treatment response, the authors should quantify colon length, histological colitis score, epithelial integrity, goblet cell depletion, mucosal cytokine expression, and ideally disease activity longitudinally after intervention. Representative H&E images are not sufficient to support claims of “normalizing histology.” Blinded quantitative scoring should be reported for colon and muscle tissue.

Response:

We sincerely thank you for this important comment regarding the need for more rigorous intestinal efficacy endpoints. We fully agree that representative H&E images alone are insufficient to support claims of histological normalization, and that quantitative assessments—including colon length measurement and blinded semi-quantitative histological scoring—are essential to strengthen the evidence for improved colitis outcomes. We have addressed this concern as follows:

Actions taken:

1. Colon length quantification added. Colon length, a well-established macroscopic indicator of colitis severity, was measured in all experimental groups. DSS treatment significantly shortened colon length compared with controls. All three interventions partially attenuated this shortening, and the combined resistance training plus anti-TNF-α group showed colon lengths approaching those of healthy controls.
2. Blinded semi-quantitative histological scoring reported. In addition to representative H&E images, we now report quantitative histological scores for colonic tissue, evaluated by two independent investigators blinded to group allocation using the predefined criteria in Table A1. The total histological score (sum of inflammatory cell infiltration, crypt architecture disruption, and mucosal ulceration/erosion subscores) is now presented for each group.
3. Remaining gaps candidly acknowledged. We acknowledge that additional intestinal endpoints—including epithelial barrier integrity assessment, goblet cell quantification, and mucosal cytokine profiling—were not performed. These are now explicitly listed as priorities for our follow-up investigations.

 

Comment 8:

The statistical reporting is inconsistent. Some sections use t statistics for multiple group comparisons after earlier describing ANOVA-based analyses. The manuscript should clearly specify when t tests, one-way ANOVA, repeated-measures ANOVA, two-way ANOVA, and post hoc tests were used. The reporting of repeated-measures ANOVA also appears unusual given the degrees of freedom and group structure; the authors should clarify whether corrections for sphericity were applied and whether individual animal trajectories were modeled appropriately. Mixed-effects models may be more suitable for longitudinal body weight and DAI data.
Response:

We sincerely thank you for this meticulous and important critique regarding the consistency and appropriateness of our statistical reporting. You are absolutely correct that the original manuscript used t statistics in some multiple-group comparison contexts where ANOVA-based analyses had been described, creating an inconsistency. We also agree that the repeated-measures ANOVA reporting requires clarification regarding sphericity corrections and model specification. We have carefully addressed each point as follows.

1. Clarification of when each statistical test was used

We have added a clear and comprehensive description in Section 2.6 (Statistical Analysis) that specifies exactly when each test was applied (Lines 290 to 312):

One-way ANOVA with Bonferroni post hoc test was used for cross‑sectional comparisons among all five experimental groups for normally distributed continuous data (e.g., muscle weight, colon length, serum biomarkers, qPCR results).

Two-way ANOVA (factorial design) was restricted to the four DSS-induced groups (DSS, DSS+Training, DSS+anti-TNF-α, DSS+Training+anti-TNF-α), with Training and anti-TNF-α as fixed factors, to assess main effects and interactions for all functional and biochemical endpoints. When a significant interaction was detected, Šídák post hoc correction was applied.

Kruskal‑Wallis test with Dunn's post hoc test and Bonferroni correction was used for non‑normally distributed or ordinal data (e.g., histological scores).

Two‑way repeated‑measures ANOVA was used for longitudinal data (body weight and DAI), with Group as a between‑subjects factor and Time as a within‑subjects factor. Mauchly's test was used to assess sphericity; when violated, the Greenhouse‑Geisser correction was applied, and corrected degrees of freedom are reported. Individual animal trajectories were modeled with Subject as the observational unit; no data imputation was required because the dataset was complete.

The t statistics reported in the Results refer to post hoc pairwise comparisons derived from the one-way or two-way ANOVA models (Tukey's or Šídák's test, respectively), not from independent Student's t-tests. To avoid any potential confusion, we have removed all individual t statistics from the pairwise comparison reports in the Results section.

2. Sphericity correction and degrees of freedom

For both body weight and DAI, we now report the outcome of Mauchly's test and the Greenhouse–Geisser epsilon. The non-integer degrees of freedom in the revised Results are the corrected values from the Greenhouse–Geisser rows of the SPSS output. Specifically:

• Body weight: Mauchly's W = 0.001, P < 0.001; ε = 0.510. The corrected time × group interaction is reported as F(16.306, 101.912) = 2.409, P = 0.076.
• DAI: Mauchly's W = 0.008, P < 0.001; ε = 0.417. The corrected interaction is reported as F(13.330, 83.315) = 7.222, P < 0.001.

3. Individual animal trajectories and model choice

The dataset was complete with no missing observations across the 8‑week period; every animal was measured at every time point. The repeated-measures ANOVA model inherently accounts for individual variability through the Subject term, and no data imputation was required. We agree, however, that linear mixed‑effects models offer greater flexibility for handling missing data, unbalanced designs, and more complex variance-covariance structures. Because our study was balanced and complete, repeated-measures ANOVA remains an appropriate method, but we have explicitly recommended mixed‑effects models for future studies with more complex longitudinal designs.

 

Comment 9:

The Bliss independence analysis is potentially interesting but not fully appropriate as currently presented. Bliss models are commonly used for pharmacological combination effects, but their application to exercise plus biologic therapy requires careful definition of effect direction, baseline, maximum possible response, and biological independence. Some effect fractions are negative, making interpretation difficult. The authors should move this analysis to the supplementary material unless they can justify the model rigorously and reconcile it with the non-significant interaction terms.

Response:

We sincerely thank you for this thoughtful and well-reasoned critique regarding the Bliss independence analysis. You are entirely correct on every point: Bliss models are primarily designed for pharmacological combination studies; their application to exercise plus biologic therapy requires careful specification of effect direction, baseline, maximum possible response, and biological independence; and the presence of negative effect fractions in our dataset makes the interpretation problematic. Most importantly, the exploratory synergy suggested by the Bliss analysis was inconsistent with the predominantly non-significant interaction terms from our two-way ANOVA. Given the interpretational challenges you identified—particularly the negative effect fractions and the difficulty in defining biological independence between resistance training and anti-TNF-α therapy—we believe that even supplementary presentation would risk confusing readers without adding meaningful value. We have therefore chosen to remove this analysis completely rather than relocate it. The Results section now relies exclusively on two-way factorial ANOVA with interaction testing and Šídák-corrected post hoc comparisons. All statements regarding the nature of the combined effects (independent and additive, with no significant interaction for most endpoints) are fully aligned with these primary analyses, eliminating the inconsistency you identified.

 

 

 

Minor Comments

1. The title should be revised. “Resistance training complements anti-TNF therapy in DSS-induced colitis by improving skeletal muscle inflammatory and mitochondrial gene signatures” would be more defensible.

Response:

We agree and have adopted the reviewer's suggested title with minor refinements to maximize precision and appeal.

 

2. The abstract overstates causality. Phrases such as “by increasing skeletal muscle oxidative phosphorylation” and “thereby potentiating anti-TNF-α therapy” should be softened unless direct mitochondrial function and interaction effects are demonstrated.

Response:

We fully agree. The offending phrases have been removed and replaced with language that accurately reflects gene-level data and the additive nature of the effects. (Lines 12 to 30)

 

3. The introduction is informative but overly expansive. It would benefit from a tighter conceptual progression from IBD-associated muscle dysfunction, to muscle immunometabolism, to the specific hypothesis being tested. Several epidemiological details could be shortened to preserve focus.

Response:

 We appreciate this guidance. We have substantially revised the Introduction to follow a tighter conceptual progression: (1) IBD and its therapeutic challenges → (2) muscle as an immunometabolic organ in IBD → (3) how resistance training may restore muscle homeostasis → (4) the specific hypothesis. Epidemiological details have been condensed, and the narrative now flows more directly toward the study rationale.  (Lines 34 to 78)

 

4. Terminology should be standardized. The manuscript alternates between infliximab, IFX, anti-TNF-α, and anti-TNF therapy. One term should be defined and used consistently.

Response:

Thank you for this suggestion. We have standardized the terminology throughout the manuscript: infliximab (IFX) is defined at first use and IFX is used thereafter when referring specifically to the drug; anti-TNF-α is used consistently for the therapeutic class, mechanism, and experimental group. All inconsistent variants have been corrected.

 

5. The phrase “bio-logic responsiveness” in the abstract appears typographically incorrect and should read “biologic responsiveness.”

Response:

We sincerely thank the reviewer for identifying this typographical error. We have corrected "bio-logic responsiveness" to "biologic responsiveness" in the Abstract.

 

6. The figures need clearer presentation. Several panels appear visually dense, and the legends do not always specify the statistical comparison being marked by each significance symbol. The authors should include exact p values where possible and clearly distinguish comparisons versus control, DSS, anti-TNF alone, or training alone.

Response:

We sincerely thank you for this important suggestion to improve the clarity of our figures. We agree that several panels were visually dense and that the figure legends did not adequately specify which comparisons were being marked by each significance symbol. We have now revised all figures and their legends to address these concerns.

Actions taken:

1. Figure legends rewritten. All figure legends now explicitly specify which statistical comparisons are being marked by each significance symbol, clearly distinguishing comparisons versus Control, versus DSS, versus anti-TNF-α alone, and versus training alone.
2. Exact P values provided where possible. We have included exact P values for the primary endpoints and key comparisons. Where space constraints prevented listing all values, the significance level is clearly tied to a specific comparison stated in the legend.
3. Visual clarity improved. Multi-panel transcriptomic figures have been simplified where possible, and axis labels and pathway names have been enlarged for readability.

.

 

7. The transcriptomic section should report sequencing depth, alignment rate, number of biological replicates, batch correction procedures, software versions, gene annotation source, and whether raw data will be deposited in a public repository.

Response:

We sincerely thank you for this important comment regarding the completeness of our transcriptomic reporting. We fully agree that these technical details are essential for reproducibility and for readers to properly evaluate the quality of the RNA-seq data. We have now substantially expanded Section 2.5 to include all requested information (Lines 262 to 289).

Actions taken:

1. Sequencing depth and alignment rate are now reported.
2. Number of biological replicates is clearly stated (n = 3 per group).
3. Batch correction procedures are described (all libraries prepared and sequenced in a single batch).
4. Software versions for key analysis tools are specified.
5. Gene annotation source (GENCODE vM25) and reference genome (GRCm38/mm10) are reported.
6. Data deposition: Raw and processed sequencing data have been deposited in the NCBI Sequence Read Archive (SRA) under BioProject ID PRJNA1366076, as already stated in the Data Availability Statement.

 

 

8. The discussion should more explicitly acknowledge limitations, including the DSS model, male-only animals, small sample size, absence of direct mitochondrial assays, absence of anti-TNF resistance modelling, and limited histological quantification.

Response:

We sincerely thank you for this important recommendation. We fully agree that the Discussion should explicitly and transparently acknowledge all relevant limitations. We have revised the Discussion to ensure that each of the following points is addressed clearly:

• Limitations of the DSS model (subacute, innate immune-driven; does not model anti‑TNF resistance, adaptive immunity, or fibrosis)
• Use of only male mice and the resulting constraint on generalizability
• Small sample size and its impact on statistical power, particularly for interaction detection
• Absence of direct mitochondrial functional assays (only gene expression data)
• Absence of anti‑TNF resistance modeling (no immunogenicity, pharmacokinetic failure, or OSM‑driven resistance)
• Limited histological quantification (semi‑quantitative scoring was performed, but goblet cell counts, epithelial barrier markers, and immunohistochemistry were not included)

We are confident that the revised Discussion fully aligns with the strength of the evidence presented.  (Lines 714 to 743)

References

1. Lopetuso, L.R.; Petito, V.; Zinicola, T.; Graziani, C.; Gerardi, V.; Arena, V.; Caristo, M.E.; Poscia, A.; Cammarota, G.; Papa, A.; et al. Infliximab does not increase colonic cancer risk associated to murine chronic colitis. World J Gastroenterol 2016, 22, 9727-9733, doi: 10.3748/wjg.v22.i44.9727.
2. Zhong, G.; Shi, R.; Chen, Q.; Zheng, Y.; Fan, X.; Sun, Y.; Wang, S.; Li, M. Metabolomics reveals the potential metabolic mechanism of infliximab against DSS-induced acute and chronic ulcerative colitis. Naunyn-Schmiedeberg's archives of pharmacology 2024, 397, 8815-8824, doi: 10.1007/s00210-024-03201-9.
   
   
3. Lourenço, Í.; Krause Neto, W.; Dos Santos Portella Amorim, L.; Moraes Munhoz Ortiz, V.; Lopes Geraldo, V.; Henrique Da Silva Ferreira, G.; Chagas Caperuto, É.; Florencio Gama, E. Muscle hypertrophy and ladder-based resistance training for rodents: a systematic review and meta-analysis. Physiol Rep 2020, 8, e14502, doi: 10.14814/phy2.14502.
4. Cao, Y.; Zhou, J.; Quan, H.; Li, W.; Li, T.; Wang, L. Resistance training alleviates muscle atrophy and muscle dysfunction by reducing inflammation and regulating compromised autophagy in aged skeletal muscle. Front Immunol 2025, 16, 1597222, doi: 10.3389/fimmu.2025.1597222.

Reviewer 4 Report

Comments and Suggestions for Authors

This manuscript investigates whether resistance training enhances the efficacy of anti-TNF therapy in a DSS-induced colitis model through modulation of skeletal muscle oxidative phosphorylation and systemic inflammation. The topic is relevant and potentially of translational interest, particularly in the context of sarcopenia in IBD. The integration of physiological, biochemical, and transcriptomic analyses is a strength. However, several important issues should be addressed to improve the rigor and clarity of the study.

Major comments:

1. Novelty and interpretation of combined effects
   The manuscript suggests that resistance training enhances anti-TNF efficacy; however, most results indicate additive rather than synergistic effects. This is also reflected in the two-way ANOVA analyses, where interaction terms are largely non-significant, while the Bliss analysis suggests partial synergy. This inconsistency should be clearly addressed, and conclusions should be moderated accordingly to avoid overinterpretation.
2. Experimental design and model clarity
   The DSS model is described as “chronic,” but the protocol appears closer to a single-cycle DSS model followed by a recovery phase. This distinction is important and should be clarified. Additionally, the relatively small sample size (n=6 per group; fewer for transcriptomics) raises concerns about statistical power, especially for detecting interaction effects.
3. Mechanistic depth
   The study relies heavily on gene expression (RNA-seq and qPCR) to support claims regarding mitochondrial function and inflammation. However, no direct functional assays of mitochondrial activity (e.g., respiration, ATP production) are provided. The authors should either include such data or clearly acknowledge this limitation and temper mechanistic claims.
4. Exercise intervention considerations
   The resistance training protocol is well described, but potential confounding factors (e.g., stress from tail loading, handling) are not discussed. Please comment on how these factors were controlled or why they are unlikely to influence the results.
5. Statistical analysis and reporting
   The statistical approach is generally appropriate, but the use of the Bliss independence model alongside ANOVA may confuse readers. The authors should clarify that the Bliss analysis is exploratory and ensure consistency in interpretation across methods.
6. Histological analysis
   Histological findings are mainly descriptive. Quantitative scoring of tissue damage and inflammation would strengthen the conclusions. In addition, higher-resolution images would improve clarity.

Minor comments:

• The Introduction is comprehensive but could be more concise and focused on the specific hypothesis.
• Some sentences throughout the manuscript are overly long or repetitive; language editing is recommended to improve readability.
• Figure legends are generally clear, but some figures (especially multi-panel transcriptomic plots) are dense and may benefit from simplification or clearer labeling.
• Please ensure consistency in terminology (e.g., “anti-TNF,” “anti–TNF-α,” “IFX”).

Comments on the Quality of English Language

The manuscript is generally understandable, but the quality of English requires improvement for clarity and readability. Several sentences are overly long and complex, which makes the text difficult to follow. There are also minor grammatical issues, inconsistent terminology (e.g., “anti-TNF,” “anti–TNF-α,” “IFX”), and occasional awkward phrasing.

I recommend careful language editing, preferably by a native English speaker or professional editing service, to improve sentence structure, conciseness, and overall clarity.

Author Response

We sincerely thank Reviewer 4 for the comprehensive and constructive evaluation of our manuscript. These detailed and insightful comments have substantially enhanced the rigor, transparency, and interpretability of our work. Below, we provide a concise summary of the key revisions made in response to each comment. All supplementary changes in the revised manuscript are indicated in purple font or by the corresponding line numbers.

 

This manuscript investigates whether resistance training enhances the efficacy of anti-TNF therapy in a DSS-induced colitis model through modulation of skeletal muscle oxidative phosphorylation and systemic inflammation. The topic is relevant and potentially of translational interest, particularly in the context of sarcopenia in IBD. The integration of physiological, biochemical, and transcriptomic analyses is a strength. However, several important issues should be addressed to improve the rigor and clarity of the study.

Comment 1: Novelty and interpretation of combined effects
The manuscript suggests that resistance training enhances anti-TNF efficacy; however, most results indicate additive rather than synergistic effects. This is also reflected in the two-way ANOVA analyses, where interaction terms are largely non-significant, while the Bliss analysis suggests partial synergy. This inconsistency should be clearly addressed, and conclusions should be moderated accordingly to avoid overinterpretation.

Response:

We sincerely thank you for your careful reading and for highlighting the inconsistency between the additive effects observed in the two-way ANOVA and the partial synergy suggested by the Bliss analysis. We fully agree that this discrepancy could lead to an overstatement of the findings, and we have taken concrete steps to resolve it and moderate our conclusions accordingly.

Actions taken:

1. The Bliss independence analysis has been completely removed from the manuscript.

The reviewer is correct that this exploratory analysis was inconsistent with the primary factorial ANOVA, which revealed predominantly non-significant interactions. Retaining it would have caused confusion and invited overinterpretation. It has been deleted from the Methods, Results, and any related discussion, in line with an earlier recommendation we received and fully support.

2. All statements regarding the combined effects have been revised to reflect independent and additive contributions.

Wherever the text previously described "synergy," "potentiation," or "superiority" without statistical justification, we now use phrasing such as "independent and additive" or "largely independent and additive." This is now the consistent terminology throughout the Results, Discussion, and Conclusions.

3. The Conclusions have been specifically tempered to avoid any implication of clinical efficacy or mechanistic synergy.

The revised Conclusions, which we include below, explicitly state that "no synergistic interaction was demonstrated" and that "they do not establish a mechanistic interaction or clinical efficacy."

We believe these revisions fully address your concern. The manuscript now presents a consistent and statistically supported interpretation of the combined intervention as additive, avoiding any overstatement.

 

 

Comment 2: Experimental design and model clarity

The DSS model is described as “chronic,” but the protocol appears closer to a single-cycle DSS model followed by a recovery phase. This distinction is important and should be clarified. Additionally, the relatively small sample size (n=6 per group; fewer for transcriptomics) raises concerns about statistical power, especially for detecting interaction effects.

Response:

We sincerely thank you for this important observation regarding the characterization of our DSS model and the statistical power of our study. We fully agree that clarity on these points is essential for appropriate interpretation of our findings. We have addressed both concerns as detailed below.

1. DSS model characterization

You are absolutely correct that the original description of the model as "chronic" was imprecise. We have revised the terminology throughout the manuscript to describe our model as a "subacute DSS-induced colitis model". This more accurately reflects the experimental protocol, which involved a single 10-day DSS exposure followed by an 8-week recovery period during which sustained systemic inflammation and muscle pathology were observed. The relevant revisions have been made in the Abstract, Introduction, Materials and Methods, Results, and Discussion sections. We appreciate you drawing our attention to this distinction.  (Lines 93 to 112)

2. Small sample size and statistical power

We acknowledge that the relatively small sample size is an important limitation that may reduce statistical power, particularly for detecting interaction effects. We have now explicitly acknowledged this limitation in the Materials and Methods (Section 2.2.2), Discussion, and Conclusions. Specifically, we state that this was an exploratory preclinical study. We further acknowledge that the limited sample size may have precluded detection of modest interaction effects, and we recommend that future studies employ larger cohorts. These revisions are now consistently reflected throughout the manuscript.  (Lines 714 to 743)

 

Comment 3: Mechanistic depth

The study relies heavily on gene expression (RNA-seq and qPCR) to support claims regarding mitochondrial function and inflammation. However, no direct functional assays of mitochondrial activity (e.g., respiration, ATP production) are provided. The authors should either include such data or clearly acknowledge this limitation and temper mechanistic claims.

Response:

We sincerely appreciate this insightful and important comment. You are absolutely correct that our study relies primarily on transcript-level evidence (RNA-seq and qPCR) to infer mitochondrial function and inflammatory status, and that direct functional assays of mitochondrial activity were not performed. We fully agree that this is a significant limitation that must be clearly acknowledged and that all mechanistic claims must be tempered accordingly.

In response, we have made the following revisions throughout the manuscript:

1. Added an explicit acknowledgment of this limitation in the Discussion.

We now state clearly that no direct functional assays of mitochondrial activity (e.g., respirometry, ATP production, enzyme activity assays) were performed, and that all inferences regarding mitochondrial oxidative phosphorylation are based on gene expression data alone. We further note that mRNA levels do not always correlate perfectly with protein abundance or enzymatic activity, and thus the functional significance of the observed transcriptional changes remains to be validated.  (Lines 735 to 739)

2. Tempered all mechanistic claims throughout the manuscript.We have systematically revised the language in the Results and Discussion to replace definitive statements such as “restored mitochondrial function” or “enhanced oxidative phosphorylation” with more cautious phrasing, such as “was associated with upregulation of mitochondrial gene expression” and “is consistent with improved oxidative phosphorylation capacity.” These revisions ensure that the distinction between transcriptional evidence and functional validation is maintained.
3. Revised the proposed mechanistic model.We now describe the proposed “muscle–immune–gut” axis as a hypothetical framework that requires direct functional validation, rather than an established mechanism.

We believe these revisions provide appropriate transparency regarding the limitations of our molecular evidence and ensure that all conclusions are properly aligned with the nature of the data presented.

 

 

Comment 4: Exercise intervention considerations

The resistance training protocol is well described, but potential confounding factors (e.g., stress from tail loading, handling) are not discussed. Please comment on how these factors were controlled or why they are unlikely to influence the results.

Response:

We thank you for this thoughtful and important point regarding potential confounding factors associated with the resistance training protocol. We agree that factors such as handling stress and the physical demands of tail loading could theoretically influence inflammatory and metabolic outcomes, and we apologize for not having addressed this in the original manuscript. We have added a dedicated description of the control measures implemented, both in the Methods and in the Discussion.  (Lines 149 to 154)

Actions taken:

We have added a paragraph explicitly detailing the strategies used to minimize and balance potential confounding effects of handling and tail loading. These include: a familiarization week without load for all mice (including those later assigned to non-training groups); progressive load increments starting at only 10% body weight; the use of foam-lined nasal clamps to minimize discomfort; and identical handling, injection, and housing conditions across all groups. Importantly, the control and DSS-only groups received the same frequency of handling and intraperitoneal injections of vehicle, ensuring that any handling-related stress was balanced across groups.

We now acknowledge that, despite these precautions, a subtle effect of chronic intermittent stress cannot be entirely excluded. However, given the balanced design and the fact that the DSS+Training group showed reduced—rather than increased—inflammatory markers relative to DSS alone, we believe it is unlikely that handling stress confounded the main findings in a direction that would create a false-positive improvement.

 

Comment 5: Statistical analysis and reporting

The statistical approach is generally appropriate, but the use of the Bliss independence model alongside ANOVA may confuse readers. The authors should clarify that the Bliss analysis is exploratory and ensure consistency in interpretation across methods.

Response:

We sincerely thank you for this comment, which aligns with an earlier concern raised during the review process. We fully agree that the inclusion of the Bliss independence model alongside the two-way ANOVA created potential confusion and led to inconsistencies in interpretation. In response to your suggestion and a similar recommendation from another reviewer, the Bliss independence analysis has been completely removed from the manuscript. It no longer appears in the Methods, Results, Discussion, Tables, or Figures. The statistical analysis now relies solely on one-way and two-way ANOVA with appropriate post hoc corrections, ensuring consistency throughout the manuscript.

Specifically, we have taken the following actions:

1. In the Methods section (2.6), all references to the Bliss independence model have been deleted. The statistical analysis is now described solely in terms of one-way ANOVA, two-way factorial ANOVA, and Šídák-adjusted post hoc comparisons.
2. In the Results section, the Bliss analysis table (former Table 2) and all associated interpretive text have been removed. Combined effects are now interpreted strictly according to the two-way ANOVA interaction terms and main effects, with no reference to exploratory synergy models.
3. The Discussion and Conclusionshave been carefully reviewed to ensure that all statements regarding the nature of the combined intervention (independent and additive, with no significant interaction) are fully consistent with the ANOVA results.

We believe this clean separation eliminates any potential confusion. We are grateful for your guidance in improving the clarity of our statistical reporting.

 

Comment 6: Histological analysis

Histological findings are mainly descriptive. Quantitative scoring of tissue damage and inflammation would strengthen the conclusions. In addition, higher-resolution images would improve clarity.

Response:

We sincerely thank the reviewer for this insightful suggestion to strengthen the histological evidence. We fully agree that quantitative scoring adds objectivity and that higher‑resolution images are essential for evaluating tissue‑level pathology. We have addressed both points through quantitative muscle and colonic histological assessments, as detailed below.
1. Muscle phenotype quantification

Quadriceps muscle mass was measured in all experimental groups. Both resistance training and anti-TNF-α therapy partially attenuated DSS-induced muscle loss. The DSS+Training group (P < 0.001) and the DSS+anti-TNF-α group (P = 0.004) showed significantly greater muscle weight than the DSS group. The combined intervention produced the greatest preservation of muscle mass (P < 0.001), which did not differ significantly from the control group (P = 0.106), indicating near-complete preservation of muscle mass.  (Lines 194 to 197; Lines 357 to 362; Lines 419 to 424)

2. Colonic histology quantification

Colon length, a well‑established macroscopic indicator of colitis severity, was measured in all groups. Colon length was significantly greater in the DSS+Training group (P = 0.001), the DSS+anti-TNF-α group (P < 0.001), and the DSS+Training+anti-TNF-α group (P < 0.001). The combination group showed values closest to those of healthy controls, although the difference between the combination group and controls remained statistically sig-nificant (P = 0.035), suggesting substantial but incomplete restoration of colon length.   (Lines 204 to 207; Lines 437 to 441; Lines 476 to 482)

3. Blinded semi‑quantitative histological scoringof colonic tissue was performed by two independent investigators using the predefined criteria in Table A1. Blinded semi‑quantitative histological scoring confirmed these observations. The total histological score (sum of inflammatory cell infiltration, crypt architecture disruption, and mucosal ulceration/erosion; range 0–12) differed significantly among the five groups (Kruskal-Wallis χ² = 26.839, P < 0.001). The DSS group showed significantly higher scores than the control group (P < 0.001). Dunn's post hoc test with Bonferroni correction revealed that total histological scores were significantly reduced in the DSS+Training+anti-TNF-α group compared with the DSS group (P = 0.004). The DSS+anti-TNF-α group also trended lower than the DSS group, though this difference did not reach statistical significance after correction (P = 0.446). The DSS+Training group did not differ significantly from DSS (P = 1.000). Notably, the combination group did not differ significantly from the control group (P = 1.000), indicating near-complete histological normalization. (Lines 465 to 475)

 

4. High‑resolution images

All histological figures were prepared from high‑resolution original captures (300 dpi). Publication‑quality image files will be submitted with the final manuscript.

 

 

 

Comment 7:

The Introduction is comprehensive but could be more concise and focused on the specific hypothesis.

Some sentences throughout the manuscript are overly long or repetitive; language editing is recommended to improve readability.

Figure legends are generally clear, but some figures (especially multi-panel transcriptomic plots) are dense and may benefit from simplification or clearer labeling.

Please ensure consistency in terminology (e.g., “anti-TNF,” “anti–TNF-α,” “IFX”).

Response:

1. The Introduction is comprehensive but could be more concise and focused on the specific hypothesis.

We agree that the original Introduction, while thorough, could be streamlined to sharpen its focus on the study hypothesis. We have revised the Introduction to reduce redundancy, tighten the narrative, and more directly lead the reader toward the specific hypothesis stated at the end. 

2. Some sentences throughout the manuscript are overly long or repetitive; language editing is recommended to improve readability.

We appreciate this observation. We have carefully reviewed the entire manuscript and revised overly long and repetitive sentences throughout. Complex sentences have been split into shorter, more focused statements, and redundant phrasing has been eliminated. Key examples include:

• Abstract: Simplified several compound sentences to improve flow.
• Introduction: Restructured dense paragraphs into more digestible units.
• Results: Shortened sentences describing statistical outcomes to clearly separate main effects, interactions, and post hoc findings.
• Discussion: Streamlined mechanistic discussions to avoid repetitive qualifications.

We believe these revisions have substantially improved the readability of the manuscript.

3. Figure legends are generally clear, but some figures (especially multi-panel transcriptomic plots) are dense and may benefit from simplification or clearer labeling.

We agree that the multi-panel transcriptomic figure (Figure 4) is inherently dense. We have revised the figure to provide more explicit guidance for navigating the panels. Additionally, we have ensured that all panel labels, pathway names, and axis titles within the figure are clearly legible. Where possible, we have simplified the presentation by focusing on the most relevant enriched pathways in the main text, with the understanding that full datasets are available via the deposited BioProject (PRJNA1366076).

4. Please ensure consistency in terminology (e.g., “anti-TNF,” “anti–TNF-α,” “IFX”).

Standardized terminology rules applied throughout:

Infliximab (IFX) is defined at first use in both the Abstract and Introduction, and IFX is used consistently thereafter when referring specifically to the drug administered in this study.

Anti-TNF-α is used consistently when referring to the therapeutic class, mechanism of action, or the experimental intervention group (e.g., DSS+anti-TNF-α group).

All variants, including "anti-TNF," "anti–TNF-α" (with en dash), and "anti-TNF therapy," have been replaced with the standardized form anti-TNF-α.

We believe these revisions have substantially improved the clarity, focus, and consistency of the manuscript. We are grateful for your careful reading and constructive suggestions.

 

 

Comment 8:

The manuscript is generally understandable, but the quality of English requires improvement for clarity and readability. Several sentences are overly long and complex, which makes the text difficult to follow. There are also minor grammatical issues, inconsistent terminology (e.g., “anti-TNF,” “anti–TNF-α,” “IFX”), and occasional awkward phrasing.

I recommend careful language editing, preferably by a native English speaker or professional editing service, to improve sentence structure, conciseness, and overall clarity.

Response:

We sincerely thank you for this candid and constructive assessment of the manuscript's language quality. We fully agree that clear, concise, and grammatically accurate writing is essential for effective scientific communication, and we appreciate your specific observations regarding overly long sentences, minor grammatical issues, inconsistent terminology, and occasional awkward phrasing.

Comprehensive language editing completed. We have carefully reviewed the entire manuscript and performed thorough language editing to improve sentence structure, conciseness, and overall clarity. Overly long and complex sentences have been split into shorter, more focused statements. Redundant or awkward phrasing has been revised for directness. Grammatical errors have been corrected. 

Terminology standardized throughout. As noted in our response to Comment 7, we have ensured consistent use of terminology: “anti-TNF-α” for the therapeutic class or mechanism, “infliximab” or “IFX” for the specific drug, and “anti-TNF-α therapy” or “anti-TNF-α treatment” for the experimental intervention. All instances have been checked and corrected. The Abbreviations section has been updated accordingly.

Professional editing service engaged. In addition to our own revisions, the revised manuscript has been reviewed by a professional scientific editing service staffed by native English speakers to ensure idiomatic expression and readability throughout.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have adequately addressed the reviewer's comments, and the manuscript has been significantly improved. I recommend acceptance of the manuscript.

Author Response

Thank you very much for your positive feedback and for recommending acceptance of our manuscript. Your time and thoughtful suggestions are greatly appreciated.

Reviewer 3 Report

Comments and Suggestions for Authors

I am happy with the new version of the manuscript.

Author Response

Thank you for your positive feedback and recommendation to accept the manuscript. We truly appreciate the time and effort you have put into reviewing our work.