Review Reports
- Chentong Wang,
- Manyang Jin and
- Xi Wang *
- et al.
Reviewer 1: Anonymous Reviewer 2: Anonymous
Round 1
Reviewer 1 Report
Comments and Suggestions for AuthorsThe manuscript investigates the effects of in ovo administration of mannan-oligosaccharides (MOS) on early growth performance, intestinal morphology, and cecal microbiota in broiler chickens. The topic is relevant and timely, particularly in the context of early-life nutritional programming and alternatives to antibiotic growth promoters. The experimental design is generally sound, and the study provides interesting data on the short-term effects of in ovo MOS administration. Nevertheless, several aspects of the manuscript require substantial improvement before it can be considered for publication.
The first issue to address is the presentation of the figures. Their current quality is insufficient for publication. The microbiota figures, particularly Figures 1–3, contain numerous panels with very small fonts and labels that are difficult to read. This considerably reduces the manuscript's readability and unnecessarily complicates the interpretation of the results. I recommend redesigning these figures by increasing the font size, improving the resolution, and considering splitting complex figures.
The interpretation of the microbiota data should also be more cautious. Throughout the Discussion, several statements imply biological mechanisms that were not directly demonstrated in the present study. Since the microbiome analysis is based on 16S rRNA sequencing, along with differential abundance and correlation analyses, the results reflect associations rather than causal relationships. Expressions suggesting that MOS "primes the neonatal gut", "supports intestinal epithelial renewal", or "steers the early cecal community" should therefore be moderated accordingly.
In my opinion, the most interesting finding of this study is that the observed effects were largely restricted to the first week after hatch. Improvements in growth performance, intestinal morphology, and microbiota composition were no longer evident at later sampling points. Surprisingly, the response's transient nature receives relatively little attention in the Discussion. Expanding this section to explain why these effects may disappear over time and discussing their biological and practical significance would considerably strengthen the manuscript.
The Spearman correlation analysis is useful as an exploratory approach; however, the Discussion occasionally overinterprets these correlations. Correlation analyses alone cannot establish functional or causal relationships between bacterial taxa and host performance. This limitation should be acknowledged more explicitly when discussing the microbiota results.
Similarly, some conclusions remain stronger than warranted by the presented data. Statements indicating that the observed physiological responses are "underpinned by" shifts in the microbiota suggest mechanistic evidence that has not been demonstrated. The conclusions would benefit from more cautious wording that consistently reflects the associative nature of the findings.
I also noticed that the manuscript reports extensive measurements of intestinal morphology but does not include representative histological images. Including representative micrographs of intestinal sections, at least for the control and the highest MOS dose, would improve the presentation of the morphological data and help readers appreciate the reported differences.
The Discussion focuses primarily on statistically significant findings, whereas the absence of treatment effects for many measured variables receives relatively little attention. Most serum biochemical parameters, intestinal morphology at later ages, and microbiota composition after 7 days remained unchanged. Discussing these negative findings would provide a more balanced interpretation of the study.
Finally, the practical relevance of the observed effects deserves further consideration. Although MOS administration improved growth performance during the first week, these differences did not persist throughout the experimental period, and no improvements in final body weight or overall feed conversion ratio were observed. A discussion of the practical implications of these transient responses under commercial production conditions would strengthen the manuscript.
The manuscript would also benefit from careful language editing. I noticed a number of grammatical, typographical, and stylistic errors throughout the text. In addition, several references do not include DOI numbers. The reference list should be carefully revised, and DOI identifiers should be added wherever available to comply with the journal's formatting requirements.
Overall, I believe this study addresses an interesting research question and presents potentially valuable experimental data. However, the manuscript requires substantial revision, particularly regarding the presentation of figures, the interpretation of microbiota findings, and the strength of the conclusions.
Author Response
|
Response to Reviewer 1 Comments
|
||
|
1. Summary |
|
|
|
Thank you very much for taking the time to review this manuscript and for all the valuable suggestions. Please find the overall and detailed responses below and the corresponding revisions highlighted in yellow in the resubmitted file, animals-4498830 R1.
|
||
|
2. Questions for General Evaluation |
Reviewer’s Evaluation |
Response and Revisions |
|
Does the introduction provide sufficient background and include all relevant references? |
Can be improved. |
We have revised according to the reviewer’s suggestions. |
|
Is the research design appropriate? |
Yes. |
Thanks. |
|
Are the methods adequately described? |
Can be improved. |
We added the statistical model description and details in the MM section. |
|
Are the results clearly presented? |
Must be improved. |
Blur figures are divided as suggested. |
|
Are the conclusions supported by the results? |
Must be improved. |
The conclusion has been improved by focusing on the current findings. |
|
Are all figures and tables clear and well-presented? |
Must be improved. |
Figures are improved with higher resolution. |
|
3. Point-by-point response to Comments and Suggestions for Authors |
||
|
General comments: The manuscript investigates the effects of in ovo administration of mannan-oligosaccharides (MOS) on early growth performance, intestinal morphology, and cecal microbiota in broiler chickens. The topic is relevant and timely, particularly in the context of early-life nutritional programming and alternatives to antibiotic growth promoters. The experimental design is generally sound, and the study provides interesting data on the short-term effects of in ovo MOS administration. Nevertheless, several aspects of the manuscript require substantial improvement before it can be considered for publication. Responses: Thank you for your affirmation, and for your valuable suggestions, which have helped us improve the quality of the manuscript.
Comment 1: The first issue to address is the presentation of the figures. Their current quality is insufficient for publication. The microbiota figures, particularly Figures 1–3, contain numerous panels with very small fonts and labels that are difficult to read. This considerably reduces the manuscript's readability and unnecessarily complicates the interpretation of the results. I recommend redesigning these figures by increasing the font size, improving the resolution, and considering splitting complex figures. |
||
|
Response 1: Sorry for the low pixel density of the figures in the previous manuscript. The original Figure 1 has been split into Figures 1–3. The original Figures 2 and 3 have also been reorganized to improve readability. We have also attached PDF versions for your convenience, in case any editing is needed.
|
||
|
Comment 2: The interpretation of the microbiota data should also be more cautious. Throughout the Discussion, several statements imply biological mechanisms that were not directly demonstrated in the present study. Since the microbiome analysis is based on 16S rRNA sequencing, along with differential abundance and correlation analyses, the results reflect associations rather than causal relationships. Expressions suggesting that MOS "primes the neonatal gut", "supports intestinal epithelial renewal", or "steers the early cecal community" should therefore be moderated accordingly. |
||
|
Response 2: We agree with you that correlation analyses just explained the strength of two phenomena happening together instead of studying their cause-and-effect. Most biological mechanisms were cited from other studies or were just speculation. We reworded all sentences you mentioned as well as the major conclusion and focused on our findings. Please find the revisions in lines 24-26, 43-46, 302-307, 345, and 392-396.
|
||
|
Comments 3: In my opinion, the most interesting finding of this study is that the observed effects were largely restricted to the first week after hatch. Improvements in growth performance, intestinal morphology, and microbiota composition were no longer evident at later sampling points. Surprisingly, the response's transient nature receives relatively little attention in the Discussion. Expanding this section to explain why these effects may disappear over time and discussing their biological and practical significance would considerably strengthen the manuscript. |
||
|
Response 3: We have discussed this point of view throughout each section of the discussion. For growth performance: "Notably, the growth benefit observed in the current trial was transient, with no effects persisting beyond 14 dph. During the perinatal period, chicks transition from yolk-derived nutrition to exogenous feed, and microbial taxa initially favored by in ovo prebiotic administration may subsequently be displaced by environmental bacteria as yolk reserves are depleted [25]." For histological measurements: "Nevertheless, in the absence of continued MOS supply, these structural improvements were not sustained at later ages." For microbiota data: "This early intestinal programming may alter the microbial community trajectory before the microbiota stabilizes. However, as with the structural improvements, the microbiota modulation was transient; by 14 dph, alpha and beta diversity did not differ between MOS-treated and control birds." We agree that this is one of the most attractive findings in the current study. Therefore, we have added further discussion about histological measurement please see lines 310-315 “After hatch, the first week represents a critical period of rapid intestinal epithelial turnover and maturation of the mucus barrier and innate immune system [30]. Interventions acting within this developmental window may confer transient morphological benefits [31]; however, as host intestinal maturation progresses and epithelial turnover dynamics change, these early advantages may gradually diminish and converge with normal developmental trajectories [32].” And the microbiota was in a separate paragraph (see lines 369–390). “Notably, by 14 and 21 dph, the cecal microbiota had stabilized across treatment groups, with no lasting differences between MOS-treated and control birds. After hatch, chicks are continuously exposed to a diverse and abundant pool of environmental microorganisms, and these environmental inputs may increasingly shape the gut microbial community during the first 1–2 weeks of life [45], potentially limiting the persistence of microbial advantages established by a single in ovo intervention. Meijerink et al. found that, regardless of whether chicks received a hen-derived microbial inoculum on the day of hatch, the microbial communities converged toward a common “mature” profile by 14 days of age [46]. Similarly, Baldwin et al. reported that the chicken gut microbiota approaches a quasi-stable state within the first week of life, after which the mature community becomes increasingly resistant to further remodeling [47]. Thus, the microbial and morphological differences observed at 7 days following in ovo administration may reflect the intervention acting during the final window before microbial community convergence. As the gut microbiota matures around 14 days of age, the early advantages conferred by a single prebiotic dosage may subsequently be attenuated through deterministic microbial succession. However, the growth-promoting and microbiota-modulating effects of this single pre-hatch intervention are transient, diminishing by 14 days post-hatch as environmental colonization and dietary transitions reshape the gut ecosystem. Our findings underscore the critical window of perinatal gut programming but also highlight the need for sustained or repeated interventions to achieve long-term performance benefits. The transient effects of in ovo MOS suggest that its benefits may be most relevant during the critical early post-hatch period.”
|
||
|
Comment 4: The Spearman correlation analysis is useful as an exploratory approach; however, the Discussion occasionally overinterprets these correlations. Correlation analyses alone cannot establish functional or causal relationships between bacterial taxa and host performance. This limitation should be acknowledged more explicitly when discussing the microbiota results. |
||
|
Response 4: We totally agree, and we have also pointed out this perspective (see lines 352–354): “Given the correlational nature of the microbiota data and the multifactorial determinants of early growth, this association may simply reflect treatment-related physiological changes rather than a direct causal relationship.”
|
||
|
Comment 5: Similarly, some conclusions remain stronger than warranted by the presented data. Statements indicating that the observed physiological responses are "underpinned by" shifts in the microbiota suggest mechanistic evidence that has not been demonstrated. The conclusions would benefit from more cautious wording that consistently reflects the associative nature of the findings. |
||
|
Response 5: Thank you for pointing this out. We agree with this comment. The conclusions in the Simple Summary, Abstract, and Discussion have all been revised accordingly.
In conclusion, in ovo administration of MOS at 0.5 mg/chick transiently improved the abundance of beneficial anaerobes and injecting 10 mg MOS could improve villus morphology and growth performance in chicks in the first week, suggesting a potential role for MOS in shaping early microbial establishment in broilers.
“In conclusion, in ovo administration of MOS at 10 mg/egg transiently improves growth, intestinal morphology, and MOS at 0.5 mg/egg altered cecal microbiota composition during the first week post-hatch, suggesting a potential role for MOS in shaping early microbial establishment in broilers. However, these effects dissipate by 14 dph as the microbiota converges toward a mature community.”
|
||
|
Comment 6: I also noticed that the manuscript reports extensive measurements of intestinal morphology but does not include representative histological images. Including representative micrographs of intestinal sections, at least for the control and the highest MOS dose, would improve the presentation of the morphological data and help readers appreciate the reported differences. |
||
|
Response 6: Thank you for the suggestion. However, we prefer to present the data numerically rather than as figures First, morphological measurements with AB-PAS staining are routine morphological assessments, and most studies in this field report such data numerically. Second, we are reluctant to select a single slide from the seven replicate slides to illustrate the findings, as this could introduce selection bias. Most importantly, numerical data offer stronger statistical power by representing the entire experimental group through means and standard errors, rather than relying on representative images.
|
||
|
Comment 7: The Discussion focuses primarily on statistically significant findings, whereas the absence of treatment effects for many measured variables receives relatively little attention. Most serum biochemical parameters, intestinal morphology at later ages, and microbiota composition after 7 days remained unchanged. Discussing these negative findings would provide a more balanced interpretation of the study. |
||
|
Response 7: Sure. We have addressed the lack of histological responses at later ages in lines 310–315. As microbial composition was our primary research interest, we have expanded the discussion to address the unchanged microbiota composition after 7 dph in a separate paragraph (see lines 369–390). We have also noted that the absence of serum biochemical responses may be attributable to the unchallenged experimental conditions (see lines 317–318). |
||
|
Comment 8: Finally, the practical relevance of the observed effects deserves further consideration. Although MOS administration improved growth performance during the first week, these differences did not persist throughout the experimental period, and no improvements in final body weight or overall feed conversion ratio were observed. A discussion of the practical implications of these transient responses under commercial production conditions would strengthen the manuscript. |
||
|
Response 8: We agree with this comment and we have added this application and see 386-390). “Our findings underscore the critical window of perinatal gut programming but also highlight the need for sustained or repeated interventions to achieve long-term performance benefits. The transient effects of in ovo MOS suggest that its benefits may be most relevant during the critical early post-hatch period.”
|
||
|
Comment 9: The manuscript would also benefit from careful language editing. I noticed a number of grammatical, typographical, and stylistic errors throughout the text. In addition, several references do not include DOI numbers. The reference list should be carefully revised, and DOI identifiers should be added wherever available to comply with the journal's formatting requirements. |
||
|
Response 9: We apologize for the typos and have asked the writing center staff to help proofread the manuscript. Although a DOI is not mandatory for Animals, we have added all necessary DOI numbers in accordance with the reviewer's suggestions. |
||
|
Comment 10: Overall, I believe this study addresses an interesting research question and presents potentially valuable experimental data. However, the manuscript requires substantial revision, particularly regarding the presentation of figures, the interpretation of microbiota findings, and the strength of the conclusions. Response 10: Thank you for your help. We corrected the manuscript according to all reviewer’s suggestions. Hope you like it. ?
|
||
|
4. Response to Comments on the Quality of English Language |
||
|
The English could be improved to more clearly express the research. |
||
|
Response: Sure. We asked help from the writing center in our university and corrected the grammar and typos.
|
||
|
5. Additional clarifications |
||
|
No other clarification. |
||
Reviewer 2 Report
Comments and Suggestions for AuthorsGeneral Comments
Dear Authors,
The manuscript presents several strengths, including a comprehensive evaluation of growth performance, intestinal morphology, serum biochemical parameters, and cecal microbiota, which provides a broad assessment of the effects of in ovo MOS supplementation. However, several issues require clarification or correction before the manuscript can be further considered for publication. My major comments are presented below.
Abstract: Please revise the Abstract according to the comments below and any modifications made to the Discussion and Conclusions.
The Introduction is well written and provides an appropriate background and rationale for the study.
The statistical analysis section requires additional detail. Please describe the statistical model more clearly, including the definition of the experimental unit, the random effects included in the model, the exact blocking structure, and how the linear and quadratic contrasts were constructed for the unequally spaced MOS doses. This is particularly important because the treatment levels (0, 0.5, 5, and 10 mg/egg) are not equally spaced, yet linear and quadratic dose responses are reported without describing the coefficients or methodology used to generate these contrasts.
Why were only approximately 280 chicks selected for the experiment?
The authors should be more cautious when integrating results across different response variables. While integrating findings is an important aspect of scientific discussion, the conclusions should accurately reflect the specific responses observed for each treatment. In the present study, the results indicate that 10 mg/egg improved feed intake, early weight gain, and duodenal morphology; 5 mg/egg reduced serum triglyceride concentration; and 0.5 mg/egg produced the most pronounced changes in the cecal microbiota.
The manuscript associates the enrichment of butyrate-producing bacteria with epithelial renewal, improved nutrient absorption, and enhanced growth. However, no measurements of short-chain fatty acids (SCFAs), gene expression, enterocyte proliferation, or other mechanistic markers were performed to support these conclusions.
Therefore, these interpretations should be presented as hypotheses or literature-supported explanations rather than as mechanisms demonstrated by the present study. Similar overinterpretations are found in several sections of the Discussion.
The Conclusions should better reflect the magnitude and duration of the observed effects. Positive responses were primarily detected at 7 days of age and did not persist until 14 or 21 days. This limitation should be emphasized, and statements suggesting long-term benefits should be avoided unless they are directly supported by the experimental data.
The manuscript contains numerous issues related to English language usage that require careful revision before publication. Examples include "protocols were approval", "performed as according to", "22 gouge needle", "flitering", "magnificence", "Statical differences", "Mechanisticaly", and "Spearmen correlation". In addition, typographical inconsistencies such as "villus he1ight" and "at older ager" were identified. Several other language and writing issues are present throughout the manuscript, reinforcing the need for a thorough professional English revision before publication.
Author Response
|
Response to Reviewer 2 Comments
|
||||
|
1. Summary |
|
|
||
|
Thank you very much for taking the time to review this manuscript and for all the valuable suggestions. Please find the overall and detailed responses below and the corresponding revisions highlighted in yellow in the resubmitted file, animals-4498830 R1.
|
||||
|
2. Questions for General Evaluation |
Reviewer’s Evaluation |
Response and Revisions |
||
|
Does the introduction provide sufficient background and include all relevant references? |
Yes. |
Thanks. |
||
|
Is the research design appropriate? |
Must be improved. |
We have added explanations regarding bird numbers, the statistical model, and data analysis details pertaining to the unequally spaced dosages." |
||
|
Are the methods adequately described? |
Must be improved. |
The same above. More details explained in step-step response. |
||
|
Are the results clearly presented? |
Yes. |
Thanks. |
||
|
Are the conclusions supported by the results? |
Must be improved. |
The conclusion has been improved by focusing on the current findings. |
||
|
Are all figures and tables clear and well-presented? |
Can be improved. |
Figures are improved with higher resolution. |
||
|
|
||||
|
3. Point-by-point response to Comments and Suggestions for Authors |
||||
|
General comments: The manuscript presents several strengths, including a comprehensive evaluation of growth performance, intestinal morphology, serum biochemical parameters, and cecal microbiota, which provides a broad assessment of the effects of in ovo MOS supplementation. However, several issues require clarification or correction before the manuscript can be further considered for publication. My major comments are presented below. Response: Thank you for your affirmation, and for your valuable suggestions, which have helped us improve the quality of the manuscript.
Comment 1: Abstract: Please revise the Abstract according to the comments below and any modifications made to the Discussion and Conclusions. |
||||
|
Response 1: Thanks. We have revised the manuscript.
|
||||
|
Comment 2: The Introduction is well written and provides an appropriate background and rationale for the study. |
||||
|
Response 2: Thank you!
|
||||
|
Comment 3: The statistical analysis section requires additional detail. Please describe the statistical model more clearly, including the definition of the experimental unit, the random effects included in the model, the exact blocking structure, and how the linear and quadratic contrasts were constructed for the unequally spaced MOS doses. This is particularly important because the treatment levels (0, 0.5, 5, and 10 mg/egg) are not equally spaced, yet linear and quadratic dose responses are reported without describing the coefficients or methodology used to generate these contrasts. |
||||
|
Response 3: Thank you for pointing these out. The statistical mode was added in lines 170-175. “ Yij = μ + αi + βj + εij, where Yij represents the above dependent variables, μ denoting population means, αi denoting injection treatment (fixed factor), βj denoting block factor (random factor), and εij denoting random error. The incubator tier location or cage location was considered as the block factor.” “The orthogonal polynomial coefficients of unequal-spaced dosage were generated by the IML procedure in SAS 9.4.” |
||||
|
Comment 4: Why were only approximately 280 chicks selected for the experiment? |
||||
|
Response 4: Sorry for the confusion. Initially, 700 eggs were incubated. To avoid potential sex effects, only male chicks were retained for growth evaluation, reducing the number to approximately 350. Since hatchability did not differ between the non-injected control and the inoculated groups (see lines 188–189), only the injected chicks were kept, yielding approximately 280 birds. With an overall hatchability of approximately 94.0%, the final number of male chicks from the inoculation treatments was 254, which were placed in 28 battery cages after hatch, with up to 10 chicks per cage. We added details about the study in lines 102-107. “A non-injected control group was included for hatchability evaluation. In the current trial, hatchability and birth weight did not differ between groups; therefore, only the injected chicks were kept for growth evaluation. To avoid potential sex effects, approximately 254 male chicks (overall hatchability 94.0%) from the inoculation treatments were placed in 28 battery cages after hatch, with up to 10 chicks per cage.”
|
||||
|
Comment 5: The authors should be more cautious when integrating results across different response variables. While integrating findings is an important aspect of scientific discussion, the conclusions should accurately reflect the specific responses observed for each treatment. In the present study, the results indicate that 10 mg/egg improved feed intake, early weight gain, and duodenal morphology; 5 mg/egg reduced serum triglyceride concentration; and 0.5 mg/egg produced the most pronounced changes in the cecal microbiota. |
||||
|
Response 5: What a solid suggestion! We fully agree, and the specific dosage has now been clearly indicated." Abstract: “In conclusion, in ovo administration of MOS at 0.5 mg/chick transiently improved the abundance of beneficial anaerobes and injecting 10 mg MOS could improve villus morphology and growth performance in chicks in the first week, suggesting a potential role for MOS in shaping early microbial establishment in broilers.” “In conclusion, in ovo administration of MOS at 10 mg/egg transiently improves growth, intestinal morphology, and MOS at 0.5 mg/egg altered cecal microbiota composition during the first week post-hatch, suggesting a potential role for MOS in shaping early microbial establishment in broilers. However, these effects dissipate by 14 dph as the microbiota converges toward a mature community.”
|
||||
|
Comment 6: The manuscript associates the enrichment of butyrate-producing bacteria with epithelial renewal, improved nutrient absorption, and enhanced growth. However, no measurements of short-chain fatty acids (SCFAs), gene expression, enterocyte proliferation, or other mechanistic markers were performed to support these conclusions. Therefore, these interpretations should be presented as hypotheses or literature-supported explanations rather than as mechanisms demonstrated by the present study. Similar overinterpretations are found in several sections of the Discussion. |
||||
|
Response 6: Yes, unfortunately we did not exam the SCFAs in this trial. As suggested, we have revised the discussion to frame these interpretations as hypotheses or literature-supported possibilities rather than as conclusions demonstrated by our data. We have also deleted those overstatements. Please see changed below: “… suggesting an expanded absorptive surface area which might be associated with efficient nutrient utilization, although this may also reflect the larger body size of treated birds. Butyrate, one of the SCFAs could be produced from MOS fermentation [26], was reported to promote epithelial cell self-renewal and differentiation via the Wnt/β-catenin and Notch signaling pathways [27]. Uni et al. (1998) reported that higher villus-to-crypt ratio indicated higher enterocyte turnover [28]. “ |
||||
|
Comment 7: The Conclusions should better reflect the magnitude and duration of the observed effects. Positive responses were primarily detected at 7 days of age and did not persist until 14 or 21 days. This limitation should be emphasized, and statements suggesting long-term benefits should be avoided unless they are directly supported by the experimental data. |
||||
|
Response 7: Sure. The conclusion has been improved by focusing on the current findings.
|
||||
|
Comment 8: The manuscript contains numerous issues related to English language usage that require careful revision before publication. Examples include "protocols were approval", "performed as according to", "22 gouge needle", "flitering", "magnificence", "Statical differences", "Mechanisticaly", and "Spearmen correlation". In addition, typographical inconsistencies such as "villus he1ight" and "at older ager" were identified. Several other language and writing issues are present throughout the manuscript, reinforcing the need for a thorough professional English revision before publication. |
||||
|
Response 8: We apologize for grammar and typos. We have sought assistance from the writing center to proofread the manuscript. |
||||
|
|
||||
|
4. Response to Comments on the Quality of English Language |
||||
|
The English could be improved to more clearly express the research. |
||||
|
Response: Sure. We asked help from the writing center in our university and corrected the grammar and typos. |
||||
|
5. Additional clarifications No other clarification.
|
||||
Round 2
Reviewer 1 Report
Comments and Suggestions for AuthorsI have carefully reviewed the revised version of the manuscript and the authors’ responses to the previous comments. The manuscript has been substantially improved, particularly in the presentation of the transient nature of the observed effects, the discussion of unchanged parameters at later ages, and the more cautious interpretation of the microbiota–performance relationships.
The study presents interesting data on the short-term effects of in ovo administration of MOS on broiler growth, intestinal morphology, and cecal microbiota. I believe that the major issues raised in the previous review have been addressed to a considerable extent. However, I still have several scientific comments that should be considered before the manuscript can be accepted.
1. The mechanistic interpretation of the microbiota findings remains somewhat stronger than supported by the experimental design.
Although the Discussion has been revised, several statements still imply mechanisms that were not directly investigated. For example, the authors state that MOS “likely underlies” the growth-promoting effects through fermentation and SCFA production, although SCFA concentrations were not measured in the present experiment. Similarly, the manuscript states that MOS treatment reduced “opportunistic pathogens” and that the observed microbial shifts support enhancement of intestinal development and growth “through modulation of the neonatal gut microbiota.”
I appreciate that the authors explicitly acknowledge that SCFAs were not measured and that the microbiota–growth relationship is correlational. Nevertheless, I recommend further moderating these statements. The current 16S rRNA data demonstrate changes in microbial composition but not altered microbial function, SCFA production, pathogen inhibition, or a causal contribution of the microbiota to growth or intestinal morphology.
In particular, terms such as “opportunistic pathogens,” “beneficial microbes,” “produce butyrate,” and “through modulation of the neonatal gut microbiota” should be used cautiously unless they are clearly presented as interpretations based on previous literature rather than findings demonstrated in the current experiment.
2. Please provide more information about the statistical criteria used for the LEfSe analysis.
The Methods currently state that LEfSe was performed with an LDA score threshold of>3.5, but the statistical significance criterion for the LEfSe analysis is not clearly described.
Please clarify:
- which statistical test was used to identify differentially abundant taxa before LDA,
- the p-value threshold applied,
- whether multiple-testing correction was performed, and
- whether the reported taxa in Figure 4 satisfied both the statistical significance and LDA thresholds.
This information is important because the manuscript interprets the identified taxa biologically, whereas microbiome differential abundance analyses involve substantial multiple testing and compositional data considerations.
I do not necessarily require the authors to repeat the entire analysis with another microbiome method, but the statistical procedure should be reported transparently , and the limitations of the approach acknowledged.
3. The discussion of practical relevance should be made more specific.
The authors have added a paragraph addressing the practical implications of the transient effects, which is appreciated. However, the current wording remains rather general: “The transient effects of in ovo MOS suggest that its benefits may be most relevant during the critical early post-hatch period.”
The actual performance data indicate that there were no significant treatment effects on final body weight, ADG, ADFI, or FCR over the full 0–21 d period.
Therefore, I suggest explicitly stating that the present results do not demonstrate a sustained production-performance benefit under the conditions of this experiment. The potential practical value of a transient first-week response should be distinguished from evidence of improved overall production efficiency.
The authors could also briefly mention that evaluation under commercial conditions, including economic considerations and potentially repeated/post-hatch supplementation, would be necessary before practical application can be assessed.
4. The conclusions should be aligned even more closely with the dose-specific results.
The revised Conclusion is substantially improved, but the wording remains somewhat broad: “suggesting a potential role for MOS in shaping early microbial establishment in broilers.”
The microbiota effects were most clearly associated with the 0.5 mg/egg treatment, whereas the strongest effects on growth and intestinal morphology were observed at 10 mg/egg. The manuscript would therefore benefit from a slightly more precise dose-specific conclusion.
I suggest emphasising that 10 mg/egg was associated with transient improvements in first-week growth and duodenal morphology, whereas 0.5 mg/egg was associated with changes in cecal microbial composition, and that these responses were not sustained at later ages. This would better reflect the actual experimental findings.
5. Histological images remain a potential improvement to the presentation.
I acknowledge the authors’ response that the quantitative measurements provide the primary evidence and that representative images may introduce selection concerns. Nevertheless, the manuscript reports substantial differences in duodenal villus height, width, and villus-to-crypt ratio at 7 dph, while no representative histological images are provided.
I therefore still consider it desirable, although not necessarily essential for acceptance, to provide representative micrographs as supplementary material, for example, from the PBS control and 10 mg/egg groups. These images would complement rather than replace the quantitative analysis.
If the authors choose not to provide them, I would accept their explanation provided that the quantitative methodology is sufficiently clear, as it currently appears to be.
The revision has substantially improved the manuscript. In particular, the authors have made a clear effort to address the transient nature of the effects and have appropriately acknowledged the correlational nature of the microbiota data. The revised manuscript is considerably more balanced than the previous version.
My remaining concerns are mainly related to the degree of mechanistic interpretation of the microbiota results and the transparency of the statistical analysis of LEfSe and correlation data. These issues should be relatively straightforward to address without additional animal experiments.
Author Response
|
Response to Reviewer 1 Comments
|
||
|
1. Summary |
|
|
|
Thank you very much for taking the time to review this manuscript and for all the valuable suggestions. Please find the overall and detailed responses below and the corresponding revisions highlighted in green in the second round of revise file, animals-4498830 R2.
|
||
|
2. Questions for General Evaluation |
Reviewer’s Evaluation |
Response and Revisions |
|
Does the introduction provide sufficient background and include all relevant references? |
Can be improved. |
The definition of prebiotics was corrected. |
|
Is the research design appropriate? |
Yes. |
Thanks. |
|
Are the methods adequately described? |
Can be improved. |
We added details about LEfSe analysis. |
|
Are the results clearly presented? |
Yes. |
Thanks. |
|
Are the conclusions supported by the results? |
Yes. |
Thanks. |
|
Are all figures and tables clear and well-presented? |
Can be improved. |
We added the histological examples per your request as a supplementary figure. |
|
3. Point-by-point response to Comments and Suggestions for Authors |
||
|
General comments: I have carefully reviewed the revised version of the manuscript and the authors’ responses to the previous comments. The manuscript has been substantially improved, particularly in the presentation of the transient nature of the observed effects, the discussion of unchanged parameters at later ages, and the more cautious interpretation of the microbiota–performance relationships. The study presents interesting data on the short-term effects of in ovo administration of MOS on broiler growth, intestinal morphology, and cecal microbiota. I believe that the major issues raised in the previous review have been addressed to a considerable extent. However, I still have several scientific comments that should be considered before the manuscript can be accepted. Responses: Thank you for your affirmation, and for your previous valuable suggestions. We future revised and improved the paper quality in the second turn of review. Hope you like it.
Comment 1: 1. The mechanistic interpretation of the microbiota findings remains somewhat stronger than supported by the experimental design. Although the Discussion has been revised, several statements still imply mechanisms that were not directly investigated. For example, the authors state that MOS “likely underlies” the growth-promoting effects through fermentation and SCFA production, although SCFA concentrations were not measured in the present experiment. Similarly, the manuscript states that MOS treatment reduced “opportunistic pathogens” and that the observed microbial shifts support enhancement of intestinal development and growth “through modulation of the neonatal gut microbiota.” I appreciate that the authors explicitly acknowledge that SCFAs were not measured and that the microbiota–growth relationship is correlational. Nevertheless, I recommend further moderating these statements. The current 16S rRNA data demonstrate changes in microbial composition but not altered microbial function, SCFA production, pathogen inhibition, or a causal contribution of the microbiota to growth or intestinal morphology. In particular, terms such as “opportunistic pathogens,” “beneficial microbes,” “produce butyrate,” and “through modulation of the neonatal gut microbiota” should be used cautiously unless they are clearly presented as interpretations based on previous literature rather than findings demonstrated in the current experiment. |
||
|
Response 1: We fully agree that 16S analysis can only characterize microbial composition and does not provide information on microbial function. Accordingly, we have moderated the strength of our original claims throughout the Discussion. Specifically, we have removed the following terms: "opportunistic pathogens," "beneficial microbes," "produce butyrate," and "through modulation of the neonatal gut microbiota."
|
||
|
Comment 2: Please provide more information about the statistical criteria used for the LEfSe analysis. The Methods currently state that LEfSe was performed with an LDA score threshold of>3.5, but the statistical significance criterion for the LEfSe analysis is not clearly described. Please clarify:
This information is important because the manuscript interprets the identified taxa biologically, whereas microbiome differential abundance analyses involve substantial multiple testing and compositional data considerations.
|
||
|
Response 2: We thank the reviewer for this valuable comment. We have now expanded our description of the LEfSe analysis. Below, we address each specific question in turn.
We applied ANOVA and Kruskal–Wallis H tests, followed by Bonferroni correction for multiple comparisons and Welch's post-hoc analysis. LEfSe is more stringent than direct comparison of relative abundance levels and additionally provides a clear cladogram visualization at different taxonomic levels. We therefore chose to present only the LDA results in the final manuscript.
We set the the significance threshold at p < 0.050.
Yes, the multiple-testing correction was performed and the more stringent method, all-against-all strategy, rather than the one-against-all approach. The differential taxa presented in Figure 4 met both criteria: LDA score > 3.5 and P < 0.050. We have added these details in MM and results sections of the second revised manuscript.
|
||
|
Comments 3: The discussion of practical relevance should be made more specific. The authors have added a paragraph addressing the practical implications of the transient effects, which is appreciated. However, the current wording remains rather general: “The transient effects of in ovo MOS suggest that its benefits may be most relevant during the critical early post-hatch period.” The actual performance data indicate that there were no significant treatment effects on final body weight, ADG, ADFI, or FCR over the full 0–21 d period. Therefore, I suggest explicitly stating that the present results do not demonstrate a sustained production-performance benefit under the conditions of this experiment. The potential practical value of a transient first-week response should be distinguished from evidence of improved overall production efficiency. The authors could also briefly mention that evaluation under commercial conditions, including economic considerations and potentially repeated/post-hatch supplementation, would be necessary before practical application can be assessed.
|
||
|
Response 3: We have removed the general statement that "the transient effects of in ovo MOS suggest that its benefits may be most relevant during the critical early post-hatch period." In addition, we have deleted any references to the overall production efficiency of MOS from the Abstract, simple summary, and Conclusion, and we have explicitly stated that overall growth performance was not affected by in ovo MOS in line 302-303. Finally, we appreciate the reviewer's consideration regarding cost, commercial conditions, and repeated use of MOS and we added them in lines 395-399.
|
||
|
Comment 4: The conclusions should be aligned even more closely with the dose-specific results. The revised Conclusion is substantially improved, but the wording remains somewhat broad: “suggesting a potential role for MOS in shaping early microbial establishment in broilers.” The microbiota effects were most clearly associated with the 0.5 mg/egg treatment, whereas the strongest effects on growth and intestinal morphology were observed at 10 mg/egg. The manuscript would therefore benefit from a slightly more precise dose-specific conclusion. I suggest emphasising that 10 mg/egg was associated with transient improvements in first-week growth and duodenal morphology, whereas 0.5 mg/egg was associated with changes in cecal microbial composition, and that these responses were not sustained at later ages. This would better reflect the actual experimental findings.
|
||
|
Response 4: In the previous version of revised manuscript (R1), we concluded that "in ovo administration of MOS at 10 mg/egg transiently improves growth and intestinal morphology, whereas MOS at 0.5 mg/egg alters cecal microbiota composition during the first week post-hatch, suggesting a potential role for MOS in shaping early microbial establishment in broilers. However, these effects dissipate by 14 days post-hatch as the microbiota converges toward a mature community" (lines 401-405). The dosage-dependent effect was already clearly stated. Furthermore, the causal relationship between in-ovo MOS and microbial composition changes is supported by our experimental design and results. Therefore, we consider that weakening the language to "be associated with" would inappropriately understate our findings. The phrase "a potential role for MOS in shaping early microbial establishment" also serves as a direct reference to our initial hypothesis. Removing this interpretative statement would reduce the conclusion to a mere repetition of the results, rather than a synthesis of our findings. |
||
|
Comment 5: Histological images remain a potential improvement to the presentation. I acknowledge the authors’ response that the quantitative measurements provide the primary evidence and that representative images may introduce selection concerns. Nevertheless, the manuscript reports substantial differences in duodenal villus height, width, and villus-to-crypt ratio at 7 dph, while no representative histological images are provided. I therefore still consider it desirable, although not necessarily essential for acceptance, to provide representative micrographs as supplementary material, for example, from the PBS control and 10 mg/egg groups. These images would complement rather than replace the quantitative analysis. If the authors choose not to provide them, I would accept their explanation provided that the quantitative methodology is sufficiently clear, as it currently appears to be.
|
||
|
Response 5: We really appreciate your help, so we went back to our images and made a supplementary figure per your request. Please see lines 210-212 and supplementary figure 1 in 222-225.
|
||
|
Overall comment: The revision has substantially improved the manuscript. In particular, the authors have made a clear effort to address the transient nature of the effects and have appropriately acknowledged the correlational nature of the microbiota data. The revised manuscript is considerably more balanced than the previous version. My remaining concerns are mainly related to the degree of mechanistic interpretation of the microbiota results and the transparency of the statistical analysis of LEfSe and correlation data. These issues should be relatively straightforward to address without additional animal experiments. Response: We thank the reviewer for the thoughtful comments. In response, we have taken the following actions to strengthen the manuscript:
We trust that these revisions have addressed the reviewer's concerns and improved the overall clarity and rigor of the manuscript.
|
||
|
|
||
|
4. Response to Comments on the Quality of English Language |
||
|
The English is fine and does not require any improvement.. |
||
|
Response: Thanks!
|
||
|
5. Additional clarifications |
||
|
Really appreciate the reviewer’s help. |
||
Reviewer 2 Report
Comments and Suggestions for AuthorsDear Authors,
Regarding the revised document and considering the items that have already been corrected, I would like to point out one remaining issue that requires clarification. The Simple Summary and Abstract state “560 Cobb 500 fertilized eggs,” whereas the Materials and Methods section reports a total of 700 eggs.
Although the experimental design and the distinction between the total number of incubated eggs and those assigned to the injected treatments can be understood after reading the full manuscript, this discrepancy may lead to ambiguity or misinterpretation when reading only the first sections of the article.
Please revise these sections to ensure consistency and clearly distinguish the total number of eggs initially incubated from the number of eggs assigned to the injected treatments.
Author Response
|
Response to Reviewer 2 Comments
|
||||
|
1. Summary |
|
|
||
|
Thank you very much for taking the time to review this manuscript and for all the valuable suggestions. Please find the overall and detailed responses below and the corresponding revisions highlighted in green in the second round of revise file, animals-4498830 R2.
|
||||
|
2. Questions for General Evaluation |
Reviewer’s Evaluation |
Response and Revisions |
||
|
Does the introduction provide sufficient background and include all relevant references? |
Yes. |
Thanks. |
||
|
Is the research design appropriate? |
Yes. |
Thanks |
||
|
Are the methods adequately described? |
Can be improved. |
We corrected the misunderstanding of egg numbers in simple summary and abstract. |
||
|
Are the results clearly presented? |
Yes. |
Thanks. |
||
|
Are the conclusions supported by the results? |
Yes. |
Thanks. |
||
|
Are all figures and tables clear and well-presented? |
Yes. |
Thanks. |
||
|
|
||||
|
3. Point-by-point response to Comments and Suggestions for Authors |
||||
|
Comment 1: Dear Authors, Regarding the revised document and considering the items that have already been corrected, I would like to point out one remaining issue that requires clarification. The Simple Summary and Abstract state “560 Cobb 500 fertilized eggs,” whereas the Materials and Methods section reports a total of 700 eggs. Although the experimental design and the distinction between the total number of incubated eggs and those assigned to the injected treatments can be understood after reading the full manuscript, this discrepancy may lead to ambiguity or misinterpretation when reading only the first sections of the article. Please revise these sections to ensure consistency and clearly distinguish the total number of eggs initially incubated from the number of eggs assigned to the injected treatments. Response: Thank you for pointing this out and we corrected the egg number in abstract and simple summary. |
||||
|
|
||||
|
4. Response to Comments on the Quality of English Language |
||||
|
The English is fine and does not require any improvement. |
||||
|
Response: Thanks. |
||||
|
5. Additional clarifications No other clarification. |
||||