Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This manuscript investigates the hepatotoxic effects of gatifloxacin (GTFX) in zebrafish larvae, proposing a non-oxidative, metabolism-driven mechanism. The study integrates morphological, histopathological, and molecular analyses, which is a strength. The topic is relevant given the environmental persistence of fluoroquinolones and their toxicological implications. However, several conceptual, methodological, and interpretational issues need to be addressed before the manuscript can be considered for publication.

The concentrations used (0.2–2.3 mg/mL) are extremely high and far exceed environmentally relevant levels (typically ng/L–µg/L range). The authors acknowledge this limitation but do not sufficiently justify the biological relevance. Please clarify: Why such high concentrations were selected beyond referencing acute toxicity. Whether these doses reflect pharmacological, toxicological, or worst-case scenarios. Include a discussion comparing your doses with reported environmental and clinical plasma concentrations.

The claim that hepatotoxicity is independent of oxidative stress is not fully supported. Only ROS (CM-H2DCFDA) was measured. Oxidative stress is a multifactorial process, involving: Antioxidant enzymes (SOD, CAT, GPx). Lipid peroxidation (MDA). Glutathione levels (GSH/GSSG). Rephrase conclusions more cautiously. Ideally include additional oxidative stress markers or clearly state this limitation.

The mechanistic claim relies mainly on mRNA expression of pparg, cyp1a, and cyp1b1. No protein-level validation (e.g., Western blot, immunostaining). No functional assays confirming: Lipid accumulation (e.g., Oil Red O staining), CYP enzymatic activity. Add supporting functional/protein data, or Tone down mechanistic claims and describe findings as associative rather than causal.

Histology was performed only for the LC10 group. This limits understanding of dose-dependent structural changes. Include at least one lower concentration group, or Justify why only LC10 was selected.

The manuscript lacks the exact p-values. Clear indication of sample size (n) in figures. It is unclear whether: Normality was tested before ANOVA. Data met assumptions for parametric tests. Improve statistical transparency and reporting.

Minor grammatical and formatting issues are present throughout. Professional language editing is advised.

Author Response

Comment 1: The concentrations used (0.2–2.3 mg/mL) are extremely high and far exceed environmentally relevant levels (typically ng/L–µg/L range). The authors acknowledge this limitation but do not sufficiently justify the biological relevance. Please clarify: Why such high concentrations were selected beyond referencing acute toxicity. Whether these doses reflect pharmacological, toxicological, or worst-case scenarios. Include a discussion comparing your doses with reported environmental and clinical plasma concentrations.

Response 1: We thank the reviewer for this important comment. Our responses to the three specific questions are as follows:

1. Why were such high concentrations selected? The tested concentrations (0.2–2.3 mg/mL) were directly derived from the acute toxicity experiment, with MNLC = 1.7 mg/mL and LC₁₀ = 2.3 mg/mL. Sub-lethal gradients (1/9 MNLC and 1/3 MNLC) were further included to capture dose‑dependent effects. This multi‑gradient concentration design has been widely adopted in zebrafish mechanistic toxicology studies (e.g., Foods 2026, 15(3), 432; https://doi.org/10.3390/foods15030432).
2. Do these doses reflect pharmacological, toxicological, or worst-case scenarios? These doses represent a toxicological worst‑case scenario designed to maximize detectable toxicological signals under survivable conditions. This is a standard paradigm in zebrafish acute toxicity mechanism studies and is not intended to mimic environmental or clinical plasma concentrations. The Zebrafish Embryo Acute Toxicity Test (ZFET) according to OECD TG 236 is an internationally recognized standard for acute toxicity assessment.
3. Comparison with reported environmental and clinical plasma concentrations. Environmental GTFX levels are typically ng/L–µg/L, and human clinical peak plasma concentrations are ~3–5 µg/mL. Our experimental concentrations (0.2–2.3 mg/mL) are 2–3 orders of magnitude higher, which is standard for acute toxicological investigations to establish points of departure (POD) for toxicity thresholds.

Changes made in manuscript:

Materials and Methods, section 2.3 line 125-128.

Comment 2: The claim that hepatotoxicity is independent of oxidative stress is not fully supported. Only ROS (CM-H2DCFDA) was measured. Oxidative stress is a multifactorial process, involving: Antioxidant enzymes (SOD, CAT, GPx). Lipid peroxidation (MDA). Glutathione levels (GSH/GSSG). Rephrase conclusions more cautiously. Ideally include additional oxidative stress markers or clearly state this limitation.

Response 2: We sincerely appreciate this rigorous comment. We agree that the CM‑H₂DCFDA assay alone cannot fully exclude all forms of oxidative stress. Since we cannot perform additional biochemical assays at this stage due to time constraints, we have therefore replaced the imprecise wording in the conclusion with a more scientifically rigorous expression. Specifically, we now state: “no statistically significant difference in bulk ROS levels was detected under the present experimental conditions”.

Changes made in manuscript:

Abstract, lines 24-27; section 3.4, lines 272-274, section 5, conclusions, lines 401-403.

Comment 3: The mechanistic claim relies mainly on mRNA expression of pparg, cyp1a, and cyp1b1. No protein-level validation (e.g., Western blot, immunostaining). No functional assays confirming: Lipid accumulation (e.g., Oil Red O staining), CYP enzymatic activity. Add supporting functional/protein data, or Tone down mechanistic claims and describe findings as associative rather than causal.

Response 3: We have substantially moderated the mechanistic claims:

We replaced strong causal language (“demonstrates”, “driven by”, “indicates”) with correlative wording (“is consistent with”, “suggests”, “may involve”).

Changes made in manuscript:

Revised title, line2-3; section 4.4, line 371-374; section 5, conclusions, line 407-409.

Comment 4: Histology was performed only for the LC10 group. This limits understanding of dose-dependent structural changes. Include at least one lower concentration group, or Justify why only LC10 was selected.

Response 4: We appreciate the reviewer’s concern. Histological analysis was performed only on the LC₁₀ group for the following reasons.

1. The LC₁₀ represents a near‑lethal exposure level where structural alterations are most pronounced, which is critical for identifying GTFX‑induced hepatotoxicity. Lower concentrations may produce subtle or non‑significant changes that would not provide definitive structural evidence.
2. Although histology was not performed on lower concentration groups, our morphological endpoints (liver area, opacity, yolk sac absorption) showed clear, dose‑dependent changes across the full concentration range (0.2–2.3 mg/mL; Figure 3). These morphological data strongly support a dose‑effect relationship.

 

Comment 5: The manuscript lacks the exact p-values. Clear indication of sample size (n) in figures. It is unclear whether: Normality was tested before ANOVA. Data met assumptions for parametric tests. Improve statistical transparency and reporting.

Response: We have now added p‑values and sample sizes (n) in all figure legends. In the revised Statistical analysis section (2.10), we clearly state that normality (Shapiro‑Wilk) and homogeneity of variances (Levene’s test) were tested before ANOVA, and appropriate parametric or non‑parametric tests were applied accordingly. All statistical assumptions were verified.

Changes made in manuscript:

section 2.10, line 211-219; Figure 3, line 254; Figure 5, line 278; Figure 6, line 289

 

Comment 6: Minor grammatical and formatting issues are present throughout. Professional language editing is advised.

Response 6: We thank the reviewer for the careful reading. The manuscript has been thoroughly proofread and edited. Specific corrections include: (1) typographical errors (e.g., “occured” → “occurred”); (2) fixed missing spaces and formatting marks; (3) split an ambiguous clause in section 2.8 for clarity; (4) unified gene/protein nomenclature and removed stray formatting. A native English speaker with expertise in environmental toxicology also reviewed the manuscript. All changes are highlighted in red in the revised version.

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript addresses the hepatotoxic effects of gatifloxacin (GTFX) in zebrafish larvae, with a particular focus on distinguishing oxidative versus non-oxidative mechanisms. The topic is relevant, especially given the increasing concern about pharmaceutical contaminants and the mechanistic understanding of drug-induced liver injury.

The study combines morphological, histological, and transcriptional endpoints in a coherent experimental framework, and the central claim, namely that hepatotoxicity occurs independently of oxidative stress, is potentially interesting. The manuscript is generally well structured and clearly written.

However, in its current form, the work remains somewhat descriptive and mechanistically limited. Several aspects of experimental design, data interpretation, and methodological detail need to be clarified or strengthened before the conclusions can be considered fully convincing.

The concentrations used (up to 2.3 mg/mL) are extremely high and far above environmentally or clinically relevant levels. While the authors acknowledge this limitation in the Conclusions, the implications are not sufficiently discussed. At such concentrations, non-specific toxicity cannot be excluded, and this weakens the mechanistic interpretation. Thus, authors should provide a stronger justification for the selected range (e.g., comparison with published zebrafish toxicity data for fluoroquinolones), discuss more critically whether the observed effects reflect general cytotoxicity rather than pathway-specific hepatotoxicity, and explicitly state how these findings can (or cannot) be extrapolated to environmental or pharmacological contexts.

The data do not fully support the conclusion that hepatotoxicity occurs independently of oxidative stress. Only a single ROS probe (CM-H2DCFDA) is used; measurements are performed at a single time point (48 h), and no antioxidant enzyme activity (e.g., SOD, CAT, GPx) or oxidative damage markers (e.g., lipid peroxidation) are assessed. Given these limitations, the absence of ROS increase cannot be taken as definitive evidence of a non-oxidative mechanism. At minimum, the authors should tone down the claim (e.g., “no detectable ROS increase under these conditions”), discuss the limitations of CM-H2DCFDA (sensitivity, specificity), and acknowledge that transient or localized oxidative stress cannot be excluded.

The mechanistic interpretation relies mainly on the upregulation of pparg, cyp1a, and cyp1b1, but these are broad, non-specific stress or metabolic markers; no functional validation is provided, and no direct measurement of lipid accumulation or metabolic flux is included. Thus, the conclusion of a “metabolism-driven hepatotoxicity” remains suggestive rather than demonstrated. The authors should moderate mechanistic claims, clarify that gene expression changes are indicative but not proof of pathway activation, and expand the Discussion to consider alternative interpretations (e.g., adaptive stress response)

Author Response

Comment 1: The concentrations used (up to 2.3 mg/mL) are extremely high and far above environmentally or clinically relevant levels. While the authors acknowledge this limitation in the Conclusions, the implications are not sufficiently discussed. At such concentrations, non-specific toxicity cannot be excluded, and this weakens the mechanistic interpretation. Thus, authors should provide a stronger justification for the selected range (e.g., comparison with published zebrafish toxicity data for fluoroquinolones), discuss more critically whether the observed effects reflect general cytotoxicity rather than pathway-specific hepatotoxicity, and explicitly state how these findings can (or cannot) be extrapolated to environmental or pharmacological contexts.

Response 1: We thank the reviewer for this insightful comment. We have revised the manuscript accordingly: (1) in Methods 2.3, we justified the concentration selection based on acute toxicity thresholds and literature comparison; (2) in Discussion 4.5, we added three lines of evidence supporting pathway‑specific effects (liver‑specific changes, selective gene upregulation, low mortality) and acknowledged that non‑specific effects cannot be fully excluded; (3) we explicitly state that these findings are not directly extrapolatable to environmental risk assessment but serve as a hypothesis‑generating basis for future studies.

Changes made in manuscript:

Section 2.3, line 125-128; section 4.5, line 374-389

 

Comment 2: The data do not fully support the conclusion that hepatotoxicity occurs independently of oxidative stress. Only a single ROS probe (CM-H2DCFDA) is used; measurements are performed at a single time point (48 h), and no antioxidant enzyme activity (e.g., SOD, CAT, GPx) or oxidative damage markers (e.g., lipid peroxidation) are assessed. Given these limitations, the absence of ROS increase cannot be taken as definitive evidence of a non-oxidative mechanism. At minimum, the authors should tone down the claim (e.g., “no detectable ROS increase under these conditions”), discuss the limitations of CM-H2DCFDA (sensitivity, specificity), and acknowledge that transient or localized oxidative stress cannot be excluded.

Response 2: We sincerely appreciate this rigorous comment. We agree that the CM‑H₂DCFDA assay alone cannot fully exclude all forms of oxidative stress. Since we cannot perform additional biochemical assays at this stage due to time constraints, we have therefore replaced the imprecise wording in the conclusion with a more scientifically rigorous expression. Specifically, we now state: “no statistically significant difference in bulk ROS levels was detected under the present experimental conditions”. This revision has been made throughout the manuscript.

Changes made in manuscript:

Abstract, line 24-26; section 3.4, line 268-270; section 5, 397-399.

 

Comment 3: The mechanistic interpretation relies mainly on the upregulation of pparg, cyp1a, and cyp1b1, but these are broad, non-specific stress or metabolic markers; no functional validation is provided, and no direct measurement of lipid accumulation or metabolic flux is included. Thus, the conclusion of a “metabolism-driven hepatotoxicity” remains suggestive rather than demonstrated. The authors should moderate mechanistic claims, clarify that gene expression changes are indicative but not proof of pathway activation, and expand the Discussion to consider alternative interpretations (e.g., adaptive stress response)

Response 3: The manuscript has been revised as follows:

All mechanistic claims have been revised from causal to associative language (e.g., “is consistent with”, “suggests” instead of “demonstrates”, “driven by”).

In Discussion section 4.4, we now explicitly state: “These transcriptional changes are associative rather than causal.”

The Conclusions have been tempered accordingly, stating that functional validation is needed in future studies.

Changes made in manuscript:

Section 4.4, line 367-369; section 5, line 403-405.

Reviewer 3 Report

Comments and Suggestions for Authors

The submitted manuscript is focused on the use of morphological, histopathological, oxidative stress and transcriptional analyses to monitor the hepatotoxic effects of gatifloxacin (GTFX) in zebrafish larvae. Given the growing problems of environmental pollution with fluoroquinolone antibiotics and their effects on liver damage, the topic is highly topical.

I have the following comments on the article:
1. The concentrations of GTFX used in the study (up to 2.3 mg/mL) are very high compared to environmental concentrations of fluoroquinolones. These usually range from ng/L to µg/L.
Therefore, it is necessary to justify the choice of concentrations, complete with a comparison with concentrations used in similar studies.
2. The manuscript states that hepatotoxicity is not mediated by oxidative stress.
This statement is not unambiguous, because DCF probes have limited specificity; antioxidant defense mechanisms were not analyzed and markers of oxidative damage to lipids or proteins were not determined (sod, gpx, cat, MDA, GSH/GSSG...). It would be necessary to reformulate the conclusions.
3. It is necessary to state how the stability of the actb reference gene was verified.
4. It would be necessary to supplement lipid staining and their quantification in order to be able to speak about steatosis or lipid accumulation.
5. It would be appropriate to supplement semi-quantitative assessment, since histological
assessment is predominantly qualitative
6. The abbreviation MNLC should be defined when first used in the results.

The manuscript will be suitable for publication after supplementing the methodological section and reformulating some interpretations and conclusions.

Author Response

Comment 1: The concentrations of GTFX used in the study (up to 2.3 mg/mL) are very high compared to environmental concentrations of fluoroquinolones. These usually range from ng/L to µg/L.
Therefore, it is necessary to justify the choice of concentrations, complete with a comparison with concentrations used in similar studies.

Response 1: We thank the reviewer for this comment. The manuscript has been revised accordingly:

The selected concentrations (0.2–2.3 mg/mL) were directly derived from the acute toxicity thresholds (MNLC = 1.7 mg/mL, LC₁₀ = 2.3 mg/mL), which is a standard design in zebrafish acute toxicity mechanism studies.

This concentration range is consistent with published acute toxicity data for other fluoroquinolones in zebrafish. For example, the 48‑h LC₅₀ of ciprofloxacin is approximately 1.5–2.5 mg/mL (Shen et al., 2019 Environ Pollut).

In Discussion section 4.5, we now explicitly state that these high concentrations represent a toxicological worst‑case scenario intended to establish a mechanistic framework, not to mimic environmental exposure. Environmental levels are typically in the ng/L–µg/L range, 2–3 orders of magnitude lower than our experimental concentrations; therefore, direct extrapolation to environmental risk assessment is not appropriate.

Changes made in manuscript:

Section 2.3, line 125-128; section 4.5, line 374-389

 

Comment 2: The manuscript states that hepatotoxicity is not mediated by oxidative stress.This statement is not unambiguous, because DCF probes have limited specificity; antioxidant defense mechanisms were not analyzed and markers of oxidative damage to lipids or proteins were not determined (sod, gpx, cat, MDA, GSH/GSSG...). It would be necessary to reformulate the conclusions.

Response 2: We agree with the reviewer. The original claim that “hepatotoxicity is independent of oxidative stress” has been revised to a more rigorous statement: “no statistically significant difference in bulk ROS levels was detected under the present experimental conditions”.

Changes made in manuscript:

Abstract, line 24-26; section 3.4, line 268-270; section 5, 397-399.

 

Comment 3: It is necessary to state how the stability of the actb reference gene was verified.

Response 3: We thank the reviewer for this comment. actb was selected as the reference gene based on its documented stability in zebrafish larvae under chemical exposure conditions (Mar. Drugs 2025, 23, 304, https://doi.org/10.3390/md23080304; PLOS ONE 17(2): e0262942. https://doi.org/10.1371/journal.pone.0262942). Moreover, the comparable Cq values of actb across all treatment groups confirmed its stable expression.

Changes made in manuscript:

Section 2.8, line 199-201

 

Comment 4: It would be necessary to supplement lipid staining and their quantification in order to be able to speak about steatosis or lipid accumulation.

Response 4: We thank the reviewer for the comment. We agree that direct lipid staining is the gold standard for confirming steatosis. Due to current time and experimental constraints, we were unable to perform this assay. After careful review, the original manuscript did not make direct claims of “steatosis” or “lipid accumulation”, but used cautious language such as “suggests” and “associated with”, supported by literature. Besides, our conclusions are based on multiple lines of indirect evidence (liver opacity, delayed yolk absorption, pparg upregulation), which are widely accepted indicators of lipid metabolic disturbance in zebrafish.

 

Comment 5: It would be appropriate to supplement semi-quantitative assessment, since histological assessment is predominantly qualitative

Response 5: We thank the reviewer for the suggestion. Although our histological assessment is primarily qualitative, it is complemented by quantitative morphological endpoints (liver area, opacity, yolk sac absorption; Figure 3). Moreover, the histological descriptions already distinguish degrees of change (e.g., “evident hepatocyte swelling”, “pronounced cytoplasmic vacuolization”), which inherently convey semi‑quantitative information. Formal semi‑quantitative scoring will be performed in future studies.

 

Comment 6: The abbreviation MNLC should be defined when first used in the results.

Response 6: We thank the reviewer for pointing this out. In Results section 3.1, we have now defined MNLC and LC₁₀ at their first use in this section.

Changes made in manuscript:

Section 3.1, line 222-224.

 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

 Accept in present form

Reviewer 2 Report

Comments and Suggestions for Authors

Dear Authors, the manuscript has been carefully revised, and thus it can be accepted in the present form.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have clarified all comments and concerns. There are no further revisions required from my end.