Hybridization-Driven Herbivorous Adaptation in Fish: Morphological, Digestive, Transcriptome, and Microbial Evidence from a Hybrid of Megalobrama amblycephala (♀) × Culter mongolicus (♂)

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The paper entitled: “Hybridization-driven herbivorous adaptation in fish: morpho-2 logical, digestive, transcriptome, and microbial evidence from a 3 hybrid of Megalobrama amblycephala (♀) × Culter mongolicus 4 (♂)” is interesting, however there are some points that should be improved and deeply revised. The statistical analysis is poorly documented, also the rearing conditions of the animals are not clear. Finally, regarding the discussion, there are a couple of things that deserve further details.

Specific suggestions are reported below:

Abstract

Acronyms should be defined in their first appearance.

Lines 38-40. Repeated concepts

Aquaculture applications?

Introduction

Line 57. I suggest a more general reference for this aspect.

Line 60. Here again the anatomy considered here considers the grass carp, however a more general description and functions are needed.

Lines 74-79. There are several studies investigating the role of microorganisms in digestion even in herbivorous fish. I suggest replacing such old references with recent materials. In addition, reference 12 was cited twice in the same spot.

Lines 85-91. It would be better to provide literature to support these concepts. Provide numbers and details about the impact of a high protein diet with respect to vegetable formulation.

Lines 97-99. All this part with clear mention of some species need literature as support.

Lines 99-111. This section seems to justify hybridization as a general solution for the carnivorous characteristics of aquaculture species; however the cited studies partially touch the topic, they rather described the consequence of a physiological/metagenomic alteration. How do the authors define hybridization as a feasible solution for aquaculture? And how could it be sustainable in terms of reproducibility? I suggest including this part in the manuscript.

Materials and Methods

Lines 133-138. I think that further information about the hybrid fish should be provided. Parent rearing condition, selection of breeders and methods applied.

Give more information about the rearing condition of the fish in the pond, how long they had shared the pond? Which were their growth rates? Furthermore, did the three types of fish live together in the same pond? How did the authors manage the animals' different feeding habits, given their different characteristics? Did they all eat the same feed?

Lines 140. How many fish were selected for type?

Line 147. How long was the fasting time before the sampling?

Line 149. Correct the formatting of the reference.

Line 161. Liver and intestinal “samples”?

Lines 164. It is not clear this part, what does it mean “the remaining intestinal tissue were sampled for histological”? the histology part was already described. Furthermore, provide additional information about microbiota sampling.

Lines 175-189. Transcriptome part lacks several crucial details, including library preparation kit used, sequencing details (read type, sequencing depth average/sample, number of biological replicates which are not specified for any analysis), but also info about data preprocessing, reference genome used and the tool.

Lines 191-201. Also for metataxonomic part, there are several things that are missing. Kit of extraction, the region of the 16S amplified (is it V3-V4?), PCR protocol used, the platform used for sequencing (is the same as transcriptomic?), bioinformatic pipeline and tools used to clean and process the data and which protocol of Picrust was used. Finally, a list of analysis performed, and the indices considered for alpha diversity and the approaches used for the beta.

Lines 203-205. PCR condition and number of samples are missing; they should be provided.

Results

Lines 208-214. I use this part as an example to say that there is no clear indication about the statistical analysis used. A paragraph in the M&M should be present.

Lines 224-235. The use of intestinal folds, which several times are used as the mucosal plicae, like the villi in mammal intestine, are quite confusing. In addition, it is something that seems quite difficult to use for a good differentiation. Does it wouldn’t be better to only consider the intestinal length?

Lines 231-233. Repetitive, already defined in lines 224-225.

Line 246. Like said before, in teleost the terminology villus is not adequate, it would be better to define them as folds.

Figure 2. The caption can be reduced and the organization of panel of figures can be improved. Columns represent the same intestinal part, while rows the same group, adding this info in the panel allow reducing the caption.

Table 2. There is an error in the content of the table. No histological values are reported.

Line 284. There is the problem related to Table 2 already mentioned.

Figure 4A. What’s the n of the PCA analysis? It should be indicated in the text.

Figure 4C. The organization of the samples and the groups in the figure is not clear. In any case I can’t see high correlation between groups. Please improve the figure and adjust the text.

Lines 304-309. This info is not properly documented; it could be useful to represent a volcano plot regarding the differentially expressed genes.

Line 325. Can the authors explain why no alpha diversity indices were analyzed?

Line 326. Can the authors define which kind of clustering was applied to the beta diversity results?

Lines 330-334. Here as before, it is not clear the statistical analysis applied to obtain this significant difference.

Line 340. How the taxa Chloroplast was considered? Why did the authors not filter from the initial dataset before the analysis?

Figure 5F. The results regarding functional abundances seem too general, the functions appear macro-categories. Also, the legend should be improved in terms of clarity. I can’t see the functions reported in lines 343-347.

Discussion

 Line 361. I think it is better to say: “This marked […] that aquaculture”.

Line 404. Why the authors define here “coils” while in the results it was used folds. I suggest homogenizing the manuscript.

Lines 412-420. Seems the quantitative data on histology were not present is difficult to support this part. The histological images did not exhibit a great reorganization of the anterior and posterior sections.   

Lines 492-494. How did the authors interpret the dominance of a Cyanobacterium, a typical autotrophic bacterium in the intestinal tract of a carnivorous fish?

Lines 504-505. I think that in these two lines there are errors regarding the references in the text. They seem like empty spaces. Please revise them.

What’s the opinion of the authors related to the tendency of the hybrid to exhibit a more herbivorous behavior and metabolic phenotype? Is it possible to give further interpretation, also from evolutive and ecological perspectives?

How did the authors interpret the difference between the results obtained with transcriptomics and microbiota? The microbiota profile exhibited a higher similarity with the herbivorous pattern, while the gene expression profiles are clearly separated among the three groups. Can the authors provide ideas about this concept. I think it could be interesting.

Conclusions

The conclusions should be ameliorated; there is only few information and low level of definition, it is too general. It is important to state the main relevant highlights of the papers, so they should be strongly improved. Also, it should be contextualized the utility and the practical application of these results in the context of the aquaculture.

Author Response

General Comment:

The paper entitled... is interesting, however there are some points that should be improved and deeply revised. The statistical analysis is poorly documented, also the rearing conditions of the animals are not clear. Finally, regarding the discussion, there are a couple of things that deserve further details.

Response: 

We thank the reviewer for the positive assessment and constructive suggestions. We have now substantially revised the statistical analysis section, clarified the rearing conditions, and expanded the discussion as detailed below.

Specific Comments

1. Abstract: Acronyms should be defined in their first appearance.

Response 1 : We thank the reviewer for this suggestion. All acronyms have now been defined at their first appearance in the Abstract.

2. Lines 38-40. Repeated concepts

Response 2 : Thank you for pointing this out. The duplicate text has been removed.

3. Aquaculture applications?

Response 3 : We have added explicit statements regarding aquaculture applications in the Abstract, as suggested.

4. Line 57. I suggest a more general reference for this aspect.

Response 4 : We have replaced the species-specific reference with a more general one.

5. Line 60. Here again the anatomy considered here considers the grass carp, however a more general description and functions are needed.

Response 5 : We have rewritten this sentence to provide a general description without focusing on a single species.

6. Lines 74-79. There are several studies investigating the role of microorganisms in digestion even in herbivorous fish. I suggest replacing such old references with recent materials. In addition, reference 12 was cited twice in the same spot.

Response 6 : We have updated the references and removed the duplicate citation.

7. Lines 85-91. It would be better to provide literature to support these concepts. Provide numbers and details about the impact of a high protein diet with respect to vegetable formulation.

Response 7 : We have added specific numbers and supporting references.

8. Lines 97-99. All this part with clear mention of some species need literature as support.

Response 8 : We have added references for each mentioned species.

9. Lines 99-111. This section seems to justify hybridization as a general solution... How do the authors define hybridization as a feasible solution for aquaculture? And how could it be sustainable in terms of reproducibility? I suggest including this part in the manuscript.

Response 9 : We thank the reviewer for this important comment. We agree that the original text was unclear in defining hybridization as a feasible and sustainable solution. We have substantially rewritten this section to define hybridization as a feasible and sustainable solution.

10. Lines 133-138. Further information about the hybrid fish... parent rearing condition, selection of breeders... rearing condition in the pond... growth rates... did all three types live together? Did they all eat the same feed?

Response 10 : We have added comprehensive details as requested.

11. Lines 140. How many fish were selected for type?

Response 11 : The sample size per type has been clarified.

12. Line 147. How long was the fasting time before the sampling?

Response 12 : The fasting time before sampling has been added.

13. Line 149. Correct the formatting of the reference.

Response 13 : The reference formatting has been fixed.

14. Line 161. Liver and intestinal “samples”?

Response 14 : Thank you for pointing this out. It has been corrected.

15. Lines 164. It is not clear this part... what does it mean "the remaining intestinal tissue were sampled for histological"?... provide additional information about microbiota sampling.

Response 15 : We have rewritten this part for clarity and added microbiota sampling details.

16. Lines 175-189. Transcriptome part lacks several crucial details... library preparation, sequencing details, biological replicates, preprocessing, reference genome, tools.

Response 16 : We have added all missing details.

17. Lines 191-201. Metataxonomic part missing details: extraction kit, 16S region, PCR protocol, platform, bioinformatics, PICRUSt2, alpha/beta indices.

Response 17 : All missing details have been added.

18. Lines 203-205. PCR condition and number of samples are missing; they should be provided.

Response 18 : We have added the PCR conditions and the number of samples.

19. Lines 208-214. No clear indication about the statistical analysis used. A paragraph in the M&M should be present.

Response 19 : We have added a dedicated statistical analysis section.

20. Lines 224-235. The use of intestinal folds... confusing. Wouldn't it be better to only consider the intestinal length?

Response 20 : We thank the reviewer for this important clarification. In fish, the“intestinal folds” (also called intestinal flexures or coils) refers to the number of bends or loops of the intestine within the abdominal cavity, which can be directly observed upon dissection (as shown in Figure 1A). This is distinct from the “mucosal folds” (or plicae) on the internal surface of the intestine. We acknowledge that the term “folds” might be ambiguous in some contexts. To avoid confusion, we have now explicitly defined in the revised manuscript that “intestinal folds” in our study refers to the gross anatomical bends/coils of the intestine, not the microscopic mucosal structures. We have also changed the term for microscopic structures from “villi” to “mucosal folds” throughout the manuscript to maintain clarity.

We respectfully disagree that this feature is difficult to use for differentiation. In fact, the number of gross intestinal folds (coils) is a classic and widely used morphological indicator for distinguishing herbivorous from carnivorous fish. Herbivorous fish typically have more intestinal folds/coils to increase food retention time, while carnivorous fish have fewer. Similar descriptions have been used in numerous previous studies (e.g., Nie & Hong, 1963; German & Horn, 2006; Li et al., 2018; Jiao et al., 2023). The difference is so pronounced that even at a glance (Figure 1A), BSB shows 7–8 folds, MC shows 2–3 folds, and BM shows an intermediate 6–7 folds. Therefore, we believe this feature is both valid and informative for assessing feeding habits.

We fully agree that relative gut length (RGL) is a more robust quantitative indicator and serves as the primary metric for evaluating feeding habits. Indeed, in our study, RGL (Table 1) is the key parameter supporting BM’s herbivorous tendency. However, we do not see a conflict between using RGL and describing gross intestinal fold counts. The two features are complementary: RGL quantifies the total length relative to body length, while fold count reflects how the intestine is arranged within the body cavity. In many cases, longer intestines also have more folds, but the fold count provides additional intuitive information that is easy to communicate and visualize (as in Figure 1A). Therefore, we have retained the fold count as a descriptive, supportive observation rather than a primary statistical indicator, while RGL remains the main quantitative measure.

21. Lines 231-233. Repetitive, already defined in lines 224-225.

Response 21 : We have deleted the repetitive lines.

22. Line 246. In teleost the terminology villus is not adequate, it would be better to define them as folds.

Response 22 :Thanks for the suggestion.We have Unified terminology throughout.

23. Figure 2. Caption can be reduced; columns represent same intestinal part, rows same group.

Response 23 : We have reorganized Figure 2 and shortened the caption.

24. Table 2. There is an error in the content of the table. No histological values are reported.

Response 24 : This was a critical error. We have corrected it, and the histological values have now been added to Table 2.

25.Line 284. There is the problem related to Table 2 already mentioned.

Response 25 : This issue has been fixed along with Table 2.

26. Figure 4A. What's the n of the PCA analysis? It should be indicated in the text.

Response 26 : Thanks. We've added the sample size (n) for the PCA analysis in the text.

27. Figure 4C. The organization... not clear. I can't see high correlation between groups. Please improve the figure and adjust the text.

Response 27 : We have improved the heatmap and adjusted the text to avoid over interpretation.

28. Lines 304-309. This info is not properly documented; it could be useful to represent a volcano plot regarding the differentially expressed genes.

Response 28 : We have added volcano plots for the differentially expressed genes.

29  Line 325. Can the authors explain why no alpha diversity indices were analyzed?

Response 29 : We thank the reviewer for raising this important point. We acknowledge that the original manuscript omitted the alpha diversity analysis of gut microbiota, which was an oversight. We have now performed a comprehensive alpha diversity analysis using the following six indices: Sobs (observed richness), Shannon (diversity), Ace (abundance-based coverage estimator), Chao (richness estimator), Coverage (Good’s coverage), and Heip (evenness). The results showed that none of the alpha diversity indices differed significantly among BSB, MC, and BM (P > 0.05 for all comparisons, Kruskal-Wallis test). This indicates that the gut microbial communities of the three fish groups are similar in terms of species richness, diversity, and evenness, despite differences in feeding habits. The lack of significant difference in alpha diversity suggests that feeding habit primarily affects community composition (beta diversity) rather than overall species richness or diversity.

We have now added these results to the Results section and the corresponding methodology to the Materials and Methods section (section 2.7). The detailed statistical results are also presented in a new supplementary table (Table 4).

We apologize for the omission and thank the reviewer for the opportunity to improve our manuscript.

30. Line 326. Can the authors define which kind of clustering was applied to the beta diversity results?

Response 30 : The clustering method (group average clustering) has been defined in the text.

31. Lines 330-334. It is not clear the statistical analysis applied to obtain this significant difference.

Response 31 : The statistical analysis has been clarified and is now described in the text.

32. How the taxa Chloroplast was considered? Why did the authors not filter from the initial dataset before the analysis?

Response 32 : We thank the reviewer for this critical methodological point. The reviewer is absolutely correct: sequences classified as Chloroplast should have been filtered out prior to analysis, as they typically originate from plant material (e.g., diet or environmental contamination) rather than from the fish gut microbiota.

In our original analysis, we did not remove Chloroplast sequences, which led to an overrepresentation of the phylum Cyanobacteria in the carnivorous MC, largely driven by the genus norank_o__Chloroplast. This was a limitation of our initial analysis.

We have revised the Materials and Methods (added filtering step), Results (updated composition data), and Discussion (acknowledged the importance of filtering) accordingly. All changes are highlighted in red in the revised manuscript.

We thank the reviewer for pointing out this oversight, which has significantly improved the quality of our microbiota analysis.

33. Figure 5F. The results regarding functional abundances seem too general... Legend should be improved. I can't see the functions reported in lines 343-347.

Response 33 : We have improved Figure 5F and its legend.

34. Line 361. I think it is better to say: "This marked [...] that aquaculture".

Response 34 : We have changed the sentence as suggested.

35. Line 404. Why the authors define here "coils" while in the results it was used folds. I suggest homogenizing the manuscript.

Response 35 : We've unified the terminology by changing "coils" to "folds" throughout the text

36. Lines 412-420. Quantitative data on histology not present... histological images did not exhibit a great reorganization of the anterior and posterior sections.

Response 36 : We have now added quantitative histological data (Table 2) and revised the discussion accordingly.

37. Lines 492-494. How did the authors interpret the dominance of a Cyanobacterium, a typical autotrophic bacterium in the intestinal tract of a carnivorous fish?

Response 37 : We thank the reviewer for this insightful question. In our original analysis, we observed a high relative abundance of the phylum Cyanobacteria in the carnivorous MC, which appeared to be dominated by the genus norank_o__Chloroplast. However, as the reviewer correctly noted, true Cyanobacteria are autotrophic bacteria that are not typically dominant in animal guts, especially in carnivorous fish. After re-examining our data, we have identified the issue: the sequences classified as “Cyanobacteria” were almost entirely derived from Chloroplasts (plant organelles), not from true autotrophic Cyanobacteria. These Chloroplast sequences originated from the plant-based components of the artificial feed or from plant material ingested incidentally during feeding.

To address this, we have now filtered out all Chloroplast and mitochondrial sequences from the OTU table prior to analysis (as also requested in Comment #32).

The previously observed “dominance” of Cyanobacteria in MC was an artifact caused by plant-derived Chloroplast sequences. We have updated the Results and Discussion accordingly, and we have added a methodological note recommending routine filtering of Chloroplast and mitochondrial sequences in fish gut microbiota studies.

We thank the reviewer for prompting this important correction, which has significantly improved the accuracy of our microbiota analysis.

38. Lines 504-505. There are errors regarding the references... empty spaces.

Response 38 : We have fixed the reference errors and removed the empty spaces as pointed out.

39. What's the opinion of the authors related to the tendency of the hybrid to exhibit a more herbivorous behavior and metabolic phenotype? Is it possible to give further interpretation, also from evolutive and ecological perspectives?

Response 39 : We thank the reviewer for this excellent suggestion. In the revised manuscript, we have added a new paragraph in the Discussion (Section 4.6) that interprets BM's herbivorous tendency from evolutionary and ecological perspectives. Evolutionarily, BM exhibits a maternally biased reversion toward the ancestral herbivorous state of cyprinids, as supported by gene expression bias (68.2% toward BSB), RIL values, and microbiota clustering. Ecologically, BM represents a generalist phenotype that combines plant‑ and animal‑digestion capacities, which likely underlies its growth heterosis and makes it well‑suited for sustainable aquaculture. Please see the revised manuscript for the full text.

40. How did the authors interpret the difference between the results obtained with transcriptomics and microbiota? The microbiota profile exhibited a higher similarity with the herbivorous pattern, while the gene expression profiles are clearly separated among the three groups.

Response 40 : This is an insightful observation. The discordance between gut microbiota and liver transcriptome patterns likely reflects different temporal and mechanistic scales of adaptation. Gut microbiota is highly plastic and responds rapidly to dietary changes (within days to weeks) and is also strongly influenced by vertical transmission and environmental sharing. BM shares its rearing environment and maternal lineage with BSB, which likely explains why its microbiota resembles BSB more closely. In contrast, liver gene expression represents a more integrated, genetically-programmed metabolic state that reflects the hybrid genome. BM’s transcriptome is clearly distinct from both parents, with 68.2% of biased genes favoring the maternal BSB but still showing unique hybrid expression patterns. This suggests that while BM harbors a ‘herbivorous-like’ microbial community (likely beneficial for plant digestion), its own metabolic program is not fully herbivorous but rather a complementary hybrid of both parental capacities, potentially explaining its superior growth (heterosis) compared to either parent. Future studies should investigate whether the microbiota drives gene expression changes or vice versa, possibly through gnotobiotic experiments or microbiota transplantation.

41. Conclusions: The conclusions should be ameliorated; there is only few information and low level of definition, it is too general. It is important to state the main relevant highlights... contextualized the utility and practical application.

Response 41 : We have completely rewritten the Conclusions section.

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript utilizes hybridization technology to breed a hybrid fish (BM) by crossing a herbivorous female Megalobrama amblycephala with a carnivorous male Culter mongolicus, attempting to reveal its dietary shifts and the underlying biological mechanisms. The study integrates multi-dimensional data, including anatomical features, digestive enzyme activities, liver transcriptome (RNA-seq), and gut microbiome (16S rRNA), ultimately concluding that the BM hybrid fish exhibits "herbivorous adaptation". Overall, the workload is adequate, and the data is abundant.However, the study falls short in exploring the deep molecular mechanisms of this dietary shift, lacking an in-depth investigation into the molecular genetic basis of the hybrid's dietary preference compared to its parental species.

1.State how many specimens were in the pond, possibly a density.

State what equipment you used to analyze the water and the method.

State how you analyzed the feed, the method, and the equipment.

2.This section would benefit from substantial revision. While the references cited are thorough and the literature review is informative, the discussion lacks integration with the study’s own findings. As a result, this portion reads more like an introduction than a critical discussion. Please revise to better connect the cited literature with your results.

3.All the fish used in the experiment are adult individuals. The dietary habits and intestinal anatomical features of fish often undergo significant changes during different stages of ontogeny. Does the BM hybrid fish exhibit a shift in dietary preference during its early developmental stages?

4.The uniform feed provided to the fish was an artificial diet (Method 2.2), and no control experiments with plant/animal-based diets were established. With only the three fish groups used as comparisons, how can it be verified that this hybrid fish is predominantly herbivorous?

5.The organ used for RNA sequencing was the liver. Under identical feeding conditions, relying solely on the enrichment prediction of KEGG pathways cannot directly prove that these expression differences are driven by a "herbivorous preference." The pathway enrichment predictions also fail to confirm whether they are directly related to dietary preference. More in-depth functional validation evidence is required.

6.Method 2.7 mentions the use of PICRUSt2 for functional prediction, which has well-known limitations. Therefore, it cannot serve as direct, independent evidence to confirm changes in intestinal metabolic function and dietary preference. To prove the authenticity and reliability of the predicted results, it is highly recommended that the authors supplement their study with metabolomics analysis.

7.The discussion on differentially expressed genes in the transcriptome is lacking.

Comments on the Quality of English Language

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

Author Response

General Comment:

This manuscript utilizes hybridization technology... Overall, the workload is adequate, and the data is abundant. However, the study falls short in exploring the deep molecular mechanisms of this dietary shift, lacking an in-depth investigation into the molecular genetic basis of the hybrid's dietary preference compared to its parental species.

Response: We thank the reviewer for acknowledging the workload and data abundance. We have substantially strengthened the molecular mechanistic discussion, added detailed DEG analysis, and acknowledged limitations where appropriate. Detailed responses follow.

1. State how many specimens were in the pond, possibly a density. State what equipment you used to analyze the water and the method. State how you analyzed the feed, the method, and the equipment.

Response 1 : All requested information has been added to the manuscript, including pond stocking density, water analysis equipment and method, and feed analysis method and equipment.

2. This section would benefit from substantial revision. While the references cited are thorough and the literature review is informative, the discussion lacks integration with the study's own findings. As a result, this portion reads more like an introduction than a critical discussion. Please revise to better connect the cited literature with your results.

Response 2 : We thank the reviewer for this critical and constructive feedback. We agree that the original Discussion section was overly descriptive of literature and did not sufficiently integrate our own findings. We have now substantially rewritten the entire Discussion following a new structure that explicitly links each literature citation to our specific results.

3. All the fish used in the experiment are adult individuals. The dietary habits and intestinal anatomical features of fish often undergo significant changes during different stages of ontogeny. Does the BM hybrid fish exhibit a shift in dietary preference during its early developmental stages?

Response 3 : This is an important limitation. We have acknowledged it and proposed future directions.

4. The uniform feed provided to the fish was an artificial diet (Method 2.2), and no control experiments with plant/animal-based diets were established. With only the three fish groups used as comparisons, how can it be verified that this hybrid fish is predominantly herbivorous?

Response 4 : We agree that this is a limitation. We have revised our claim to “herbivorous tendency” rather than “herbivorous” and added a clear acknowledgment.

5. The organ used for RNA sequencing was the liver. Under identical feeding conditions, relying solely on the enrichment prediction of KEGG pathways cannot directly prove that these expression differences are driven by a 'herbivorous preference.' The pathway enrichment predictions also fail to confirm whether they are directly related to dietary preference. More in-depth functional validation evidence is required.

Response 5 : We agree and have added both a clear caveat and additional supportive data. While we agree that transcriptome data alone cannot prove causal preference, our conclusions are drawn from the convergence of multiple independent lines of evidence: morphology (herbivore-like RIL), digestive physiology (higher amylase), microbiota (herbivore-like composition), and transcriptomics. This multi-omics consistency strongly supports the herbivorous tendency of BM, even though causal proof would require functional validation (e.g., gene knockout).

6. Method 2.7 mentions the use of PICRUSt2 for functional prediction, which has well-known limitations. Therefore, it cannot serve as direct, independent evidence... It is highly recommended that the authors supplement their study with metabolomics analysis.

Response 6 : We acknowledge the limitations of PICRUSt2 and the value of metabolomics. Due to resource constraints, we cannot add metabolomics at this stage, but we have: (1) clearly stated the limitation; (2) presented PICRUSt2 results as hypothesis-generating; (3) Importantly, the PICRUSt2-predicted higher carbohydrate metabolism in BSB and BM is cross-validated by our direct measurements of significantly higher α-amylase activity in these groups (Figure 3A), strengthening the biological plausibility of the prediction.

7. The discussion on differentially expressed genes in the transcriptome is lacking.

Response 7 : Thanks for the comment. We have added a comprehensive new subsection on DEGs.

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I acknowledge the authors' efforts to address the requests raised in the first round of corrections. However, there remain a few small issues that would be worth addressing before the deserved publication. I'll leave a few comments here:

Lines 53-56. I saw you put the sentence more general, and this is good, however I also suggested to replace the reference (3), as it is about grass carp specifically. You can choose something more general, as a description.

Lines 58-59. Same comment as before, the reference is related with carp. I can’t see any changes in the text with respect to the previous version of the manuscript.

Lines 146-154. I saw the corrections made, but the question remains. Thinking about the parents only, why the authors provided the same diet for a carnivorous and an herbivorous fish (BSB, MC)? I appreciated you inserted this fact as a limitation in the analysis.

Line 411. I am not convinced about the clustering at phylum level. I was wondering why the authors decided to cluster samples at this taxonomic ranking? and not with genera, which could have provided a more complex and diverse profile, with more taxa to consider. It's not wrong, just curious.

Lines 416- 429. Several efforts have been made to clarify the statistical part, but I can’t see the description of the analysis (I believe that is a Kruskall-Wallies test) among the obtained OTUs and Phyla. Please add this information to the text.

Regarding Response 40: As already said, I appreciated the addition of the “Integrative perspective and limitations” paragraph. And so, I think you could also add further details about this response to the main text.

Author Response

We thank the reviewer for their careful re-evaluation of our revised manuscript and for acknowledging our efforts in the first round of corrections. We have now addressed all remaining issues point‑by‑point as detailed below. All modifications in the revised manuscript are highlighted using bold text or track changes for easy identification.

Comments 1：Lines 53-56. I saw you put the sentence more general, and this is good, however I also suggested to replace the reference (3), as it is about grass carp specifically. You can choose something more general, as a description.

Response 1: We thank the reviewer for this constructive suggestion. We agree that a more general reference is preferable in this context. Accordingly, we have replaced the original reference [3] (which focused specifically on grass carp) with two new references that provide a broader description of digestive enzyme activities in relation to feeding habits in fish.

Comments 2：Lines 58-59. Same comment as before, the reference is related with carp. I can’t see any changes in the text with respect to the previous version of the manuscript.

Response 2:We apologize for misunderstanding the precise location of the requested change in the first revision. Accordingly, we have replaced reference [4] with a general reference on fish alimentary canal morphology (Purushothaman et al., 2016) that describes the three‑segment division across multiple species.We thank the reviewer for their patience and for clarifying the exact location.

Comments 3：Lines 146-154. I saw the corrections made, but the question remains. Thinking about the parents only, why the authors provided the same diet for a carnivorous and an herbivorous fish (BSB, MC)? I appreciated you inserted this fact as a limitation in the analysis.

Response 3:We thank the reviewer for acknowledging the limitation paragraph. To further clarify the rationale behind feeding the same diet to both parental species and the hybrid, we have added a brief explanation in the Methods section (2.2 Experimental fish sources). The key reason is to control for dietary variation so that any observed differences in digestion, metabolism, and microbiota can be attributed to genetic factors rather than diet. This common practice in hybrid physiology studies allows direct comparison of intrinsic digestive capacities. We have also retained the limitation statement in the Discussion (section 4.6) as suggested.

Comments 4：Line 411. I am not convinced about the clustering at phylum level. I was wondering why the authors decided to cluster samples at this taxonomic ranking? and not with genera, which could have provided a more complex and diverse profile, with more taxa to consider. It's not wrong, just curious.

Response 4:We thank the reviewer for this thoughtful question. We chose to present beta diversity clustering at the phylum level for two main reasons:

1. Clarity of major community shifts – At the phylum level, the differences among BSB, MC, and BM are very clear (e.g., Fusobacteriota dominance in BSB/BM vs. low abundance in MC), which directly supports our main conclusion about herbivory‑associated microbiota.
2. Complementary genus‑level analysis – We do present genus‑level composition in Figure 5E (e.g., Cetobacterium dominance), and the beta diversity analysis at the genus level (data not shown) yields essentially the same clustering pattern. However, genus‑level profiles contain many low‑abundance taxa that can introduce noise, making the phylum‑level visualization more robust for the main message.

Comments 5：Lines 416- 429. Several efforts have been made to clarify the statistical part, but I can’t see the description of the analysis (I believe that is a Kruskall-Wallies test) among the obtained OTUs and Phyla. Please add this information to the text.

Response 5: We apologize for the omission. The statistical test used for alpha diversity comparisons (Sobs, Shannon, Ace, Chao, etc.) was indeed the Kruskal‑Wallis test, followed by Dunn’s post‑hoc test for pairwise comparisons. This information was originally present only in the Methods section (2.7). We have now also added it explicitly in the Results section (3.6) where the alpha diversity indices are presented.

Comments 6：Regarding Response 40: As already said, I appreciated the addition of the “Integrative perspective and limitations” paragraph. And so, I think you could also add further details about this response to the main text.

Response 6: We thank the reviewer for appreciating the “Integrative perspective and limitations” paragraph (section 4.6). In response to this comment, we have expanded that paragraph to include more detailed evolutionary and ecological interpretations that were originally summarized in Response 40. Specifically, we have added: 

An evolutionary perspective explaining why BM displays a maternally biased reversion toward the ancestral herbivorous state within Cyprinidae.

An ecological perspective highlighting the generalist / intermediate strategy that may confer advantages in fluctuating environments and aquaculture settings.

A more explicit statement that the carnivorous adaptations of MC may be genetically recessive or overridden by conserved herbivorous regulatory networks from BSB.

Reviewer 2 Report

Comments and Suggestions for Authors

The author has made some revisions based on the previous feedback.

Line 105: Reference format [18,21]
Line 110: The symbol after "behavior"
Lines 168, 500, 504: Error indicating that the citation source cannot be found?
Lines 234–261: The description of the method content is too lengthy; it is recommended to summarize and condense it.
Line 432: Table 44? 

There is still room for further revision in the discussion section.

Comments on the Quality of English Language

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

Author Response

Dear Editor and Reviewers,

We thank the reviewer for their careful re-evaluation of our revised manuscript and for acknowledging our efforts in the first round of corrections. We have now addressed all remaining issues point‑by‑point as detailed below. All modifications in the revised manuscript are highlighted using bold text or track changes for easy identification.

Comments and Suggestions for Authors

The author has made some revisions based on the previous feedback.

Comments 1：Line 105: Reference format [18,21]

Response 1: We apologize for the formatting error. We have now corrected the format to “[21]” .

Comments 2 Line 110: The symbol after "behavior"

Response 2: We thank the reviewer for noticing this typographical error. We have removed the extraneous symbol and ensured the punctuation is correct.

 Comments 3 Lines 168, 500, 504: Error indicating that the citation source cannot be found?

Response 3: We apologize for the missing or incorrectly formatted citations at these line numbers. All references cited in the text are now present in the reference list, and no “citation source not found” errors remain.

Comments 4 Lines 234–261: The description of the method content is too lengthy; it is recommended to summarize and condense it.

Response 4:We agree that the method description for gut microbiota sequencing (section 2.7) was overly detailed. We have condensed this section by removing redundant explanations of standard steps (e.g., detailed PCR cycling, QIIME2 steps that are common knowledge) and keeping only essential parameters. The length has been reduced by approximately 40% while retaining all critical information.

Comments 5 Line 432: Table 44?

Response 5:The correct reference is Table 4. We have corrected it accordingly.

Comments 6There is still room for further revision in the discussion section.

Response 6:We thank the reviewer for the suggestion to further revise the Discussion section. In response, we have carried out a thorough revision of the entire Discussion (Section 4) with the following improvements:

Reduced redundancy. Removed repetitive statements that restated results already clearly presented in the Results section. 

Improved logical flow. Added clear topic sentences and transitional phrases between paragraphs.

Strengthened key messages. Explicitly stated how BM differs from both parents in each domain, and how each domain supports the herbivorous tendency or improved growth.

Language polishing. Corrected awkward expressions, improved conciseness, and ensured consistent use of scientific terminology.

We believe the revised Discussion is now more coherent, impactful, and suitable for publication. Changes are highlighted in bold or with track changes in the revised manuscript.