JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-04111-7 (2025)

Title: Predictive Role of the Albumin-Bilirubin Score in ICU Patients with Cirrhosis and Sepsis:
Insights from a Large Retrospective Cohort
Version: 1 Date: 01 Jun 2025
Reviewer's report:
Thank you for addressing my concerns. I have further queries:
1. The authors have included renal failure as covariates for the study. However, neurological
failure remains omitted.  Please clarify.
2.  Please provide clarification in the main text on the pairwise comparisons survival that was
only statistically significant for T3 vs lower Ts but not lower T2 vs T1.
3. The authors have added a short discussion on the effect of diabetes on liver function, systemic
inflammation and immune response. It would be beneficial to elaborate on this and provide the
appropriate references.
Review for 10.1186/s12876-025-04111-7 (2025)

Title: Predictive Role of the Albumin-Bilirubin Score in ICU Patients with Cirrhosis and Sepsis:
Insights from a Large Retrospective Cohort
Version: 2 Date: 17 Jun 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-04111-7 (2025)

Title: Predictive Role of the Albumin-Bilirubin Score in ICU Patients with Cirrhosis and Sepsis:
Insights from a Large Retrospective Cohort
Version: 2 Date: 21 Jun 2025
Reviewer:  Iliana Mani
Reviewer's report:
Authors addressed my concerns adequately. I have no further comments to make
Review for 10.1186/s12876-025-04123-3 (2025)

Title: Combined association of Chewing Capacity and Depression with Constipation: A Cross-
Sectional Study
Version: 1 Date: 15 May 2025
Reviewer's report:
The authors assessed the combined association of chewing capacity and depression with
constipation. Below I summarize my recommendations:
1# The author states in the introduction that the reason for conducting this research is: "Since
both factors are prevalent among aging populations, understanding their combined influence
could provide critical insights for targeted interventions." However, it can be observed from
the results section that the research was not conducted within the elderly population, and the
methods section does not explain the age range of the participants in this study.
2# The exclusion criteria are unclear and described imprecisely as “or other relevant covariates.”
Figure 1 or the main text should clearly show which study participants were excluded to ensure
transparency for the readers.
3# For some variables, such as uric acid, creatinine, and total bilirubin, is there evidence to
support their adjustment as confounding factors?
4# The inclusion and exclusion criteria for participants are somewhat confusing. The
author excluded participants with missing data for certain variables, such as hypertension,
cardiovascular disease (CVD), and hyperlipidemia. While the methods section provides
definitions for hypertension and CVD, it does not specify the diagnostic criteria for
hyperlipidemia. Furthermore, these three variables were not adjusted for as confounding factors.
In addition, diabetes, which was adjusted for as a confounder, also lacks an explanation of its
diagnostic criteria.
5# Additionally, the author did not consider several key factors that significantly affect
constipation, such as diet and physical activity.
6# Although the author labels Table 1 as “Weighted characteristics of participants,” there
is no indication in the methods section that the complex sampling design of NHANES—
including weights, clustering, and stratification—was taken into account. Moreover, based on
the description of the statistical methods and the presentation of results in Table 1, it appears
that the author likely conducted a conventional analysis rather than a weighted one.
7# The sensitivity analysis and mediation analysis are not adequately described in the statistical
methods section.
Review for 10.1186/s12876-025-04120-6 (2025)

Title: Machine Learning Survival Models for Non-alcoholic Fatty Liver Disease Based on a
Health Checkup Cohort
Version: 0 Date: 27 May 2025
Reviewer:  Monica Mischitelli
Reviewer's report:
Authors explore the possibility to use a random survival forests (RSF) model to better investigate
the distribution of NAFLD risk and time.
The study is really interesting, nevertheless, I think revisions are required.
First: it needs to better describe study population, how were subjects who followed diets
considered? For example, were celiac subjects or those with particular food allergies excluded?
Were pregnant women excluded from the study? How many grams of alcohol does medium/
heavy consumption correspond to? What is the questionnaire administered based on? How were
glucose intolerance and insuline resistance treated?
I also believe it is absolutely necessary to specify why some blood count parameters were chosen.
I understand the value of platelets that, in subjects affected by fatty liver disease, contribute
to the creation of a persistent low grade inflammatory state, on the other hand I believe that
it is absolutely necessary to clarify the choice of the use of red blood cells, hemoglobin and
the remaining parameters of the blood count, especially white blood cells included in the top
5 variables in the RSF.
I also think it is quite obvious that BMI and lipid profile work as good predictors, I would instead
like to better clarify the role of liver function indices and why renal function indices were also
investigated.
Finally, it would be useful to specify the type of parameter that allowed to evaluate the enrolled
subjects as NAFLD-free or affected by NAFLD after 3 years of follow-up.
In conclusion, given the numerous and highlighted limitations of the study, I believe it is
necessary to better describe the study cohort and argue more precisely the choice and utility of
the predictors included in the population stratification model.
Review for 10.1186/s12876-025-04120-6 (2025)

Title: Machine Learning Survival Models for Non-alcoholic Fatty Liver Disease Based on a
Health Checkup Cohort
Version: 1 Date: 22 Jun 2025
Reviewer:  Monica Mischitelli
Reviewer's report:
The authors revised the manuscript according to the suggestions, but some adjustments are still
needed:
1) specify whether subjects with particular food allergies have been excluded
2) pregnant women instead of pregnant female in the study population paragraph
3) specify how many grams of alcohol corresponds to a medium/strong consumption
4) on what principles is the health control questionnaire administered based?
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 3 Date: 25 Jan 2025
Reviewer's report:
I read with interest the article entitled " Impacts of Salt Restriction on Nutritional Status,
Sarcopenia, and Mortality of Cirrhotic Patients With Ascites". The study is interesting, However:
-- Abstract: It is important to report on the results the effect of salt restriction on control of
ascites, not merely on sarcopenia and mortality
--Introduction: You should illustrate more the gap of knowledge in this area of research.
--Methods: Sample size calculation and power of the study are important to better validate the
results of the study.
--Results: Well illustrated.
--Discussion: More studies are needed to better enrich the discussion.  You should illustrate
more the strengths and limitations of the study.
--Conclusions: You should add the implications of the study on our current knowledge. It is
important to report the effect of salt restriction on control of ascites?
• References: More references are needed to enrich introduction and discussion. References
are few regarding the importance of the topic with many of the references are old/ I suggest
relevant and recent references e.g. PMID: 27512927, PMID: 33369880, PMID: 29182438,
PMID: 31448717, PMID: 28082116.
• English language needs minor polishing through the whole manuscript.
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 3 Date: 30 Jan 2025
Reviewer's report:
It is very interesting yet controversial research which give us many insight on the effect of salt
restriction.
However , the numbers of mortality that exceed 20 percent during 6 month also brings question
is it merely due to salt restrictions or there's another confounding factor that might interfere with
the results.
I think the research procedure on how the follow up and data collection need to be clarify
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 3 Date: 05 Feb 2025
Reviewer's report:
Comments to the Authors
1. This study did not elaborate on a salt-restricted diet, such as the specific value of daily salt
intake.
2. Evaluating the effect of ascites management only by the frequency of abdominal paracentesis
without taking into account factors such as the volume and nature of ascites cannot accurately
determine the true impact of salt-restriction on ascites management.
3. The three-month follow-up period may not fully assess the long-term effects of salt-restricted
diets nor determine the long-term efficacy and safety of salt-restricted diets.
4. In the methods section of the abstract, the follow-up time is mentioned as 6 months, whereas
in the subsequent text, the follow-up time is stated as 3 months. Please correct this discrepancy.
5. In this article, when professional term abbreviations first appear, their full forms should be
used. (For example, LVP, SBP, GI, etc.)
6. This study is a prospective design. Please supplement the informed consent form of the
patients.
7. Please conduct a K-M survival analysis in the results of the study.
8. The structure of the results section is disorganized. Please make the necessary revisions.
9. Please explain whether sarcopenia in patients with cirrhotic ascites exists at baseline or
develops during follow-up period.
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 3 Date: 06 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-Although the study is prospective, the lack of random assignment to diet groups raises concerns
about selection bias. The groups are determined based on dietary adherence (as assessed by
questionnaires and urine tests), but without randomization, it is difficult to definitively control
for confounding factors that may influence outcomes (e.g., severity of cirrhosis, comorbid
conditions).
-The exclusion of patients with specific comorbidities (e.g., diabetes, chronic kidney disease) is a
reasonable approach, but there may still be other confounding factors that influence both dietary
adherence and the outcomes measured. These could include socioeconomic status, baseline liver
function, or even subjective factors like patient motivation and lifestyle, which are difficult to
fully control.
-The study mentions a three-month follow-up period, but this may be insufficient to fully capture
long-term changes in nutritional status and muscle mass. Cirrhotic patients with ascites can
have prolonged disease progression, and three months may not be enough to observe significant
changes in mortality or nutritional health, especially in those with advanced cirrhosis.
-The study is focused on observational outcomes such as nutritional status, sarcopenia, and
mortality, but the underlying biological mechanisms through which sodium restriction affects
these outcomes are not explored. Future research could benefit from investigating biochemical
markers (e.g., inflammation, muscle protein synthesis) or hormonal changes (e.g., aldosterone,
cortisol) that could help explain the observed associations.
-The authors effectively highlight that fluid retention complicates body composition
measurements, especially in the SUD group. However, there could be more emphasis on the
challenges of interpreting bioelectrical impedance results in the context of fluid overload. Since
the SUD group had significantly higher total body water (TBW), the authors could clarify further
how this fluid retention may mask the true nutritional status or muscle mass in these patients.
-The authors do well to note the critical role of nutritional support in mitigating the effects of
sodium restriction. However, it would be helpful to explore in more detail the type of nutritional
support that might be most beneficial for cirrhotic patients on a salt-restricted diet. Are there
specific dietary interventions (e.g., higher protein intake, supplementation) that could help
reduce the negative impact of sarcopenia?
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 6 Date: 26 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03830-1 (2025)

Title: Impacts of Salt Restriction on Nutritional Status, Sarcopenia, and Mortality of Cirrhotic
Patients With Ascites
Version: 6 Date: 05 Mar 2025
Reviewer's report:
Comments to the Authors
1.The authors should add multivariate analysis to account for differences in mortality, disease
development, and the effects of a salt-restricted diet between the two groups.
Review for 10.1186/s12876-025-04008-5 (2025)

Title: Neonatal Intrahepatic Cholestasis Caused by Citrin Deficiency: Clinical Features, Genetic
Characteristics, and Treatment Outcomes
Version: 5 Date: 18 Apr 2025
Reviewer's report:
Dear authors,
Thank you for the revised version of the manuscript. All open questions and remarks have been
address and the  manuscript has been revised accordingly. however, several minor issues remain
that require correction before publication:
Incorrect spacing and punctuation are still present throughout the manuscript.
Lines 72, 167, 195, and elsewhere: The gene symbol "SLC25A13" should be italicized
consistently.
Line 88: The variant notation “c.1177+1G4A” is incorrect. Please revise according to standard
nomenclature.
Line 124: Replace “whole-exon sequencing” with the correct term “whole exome sequencing.”
Line 160: The sentence "Notably, none of the infants exhibited pruritus" may be ambiguous
since infants cannot verbally report pruritus. Consider rephrasing this sentence to indicate clearly
the absence of observable indirect signs (e.g., scratching or skin irritation).
Line 174: Correct variant notation from “(p.R467)*” to the standard form “(p.R467*)”.
Line 202: Use standard notation “c.852_855del/c.615+5G>A” instead of “c.852_855del
+c.615+5G>A”.
Lines 207 and 297: Replace “c.1399C>T+c.1638_1660dup case” with “the case with compound
heterozygous c.1399C>T/c.1638_1660dup.”
Lines 219 and 264: Change “c.852_855del+c.615+5G>A compound heterozygotes” to
“individuals who were compound heterozygous for c.852_855del/c.615+5G>A.”
Lines 223 and 284: Confirm consistent usage of “compound heterozygous c.1399C>T/
c.1638_1660dup.”
Line 226: Correct punctuation error "disorder“.".
Standardize the variant naming convention, as currently there are inconsistencies
(“c.851_854del,” “851-854del,” and “c.851_854del4”). Confirm and correct to standard
nomenclature. Please clarify whether “c.851_854del” and “c.852_855del” represent the same
variant (rs80338720).
Line 257: Specify clearly the ACMG criteria fulfilled (e.g., PM2, PM3).
Reference 7 is incorrect. Please revise all references thoroughly according to journal guidelines.
Table 1 and its supplementary material: Correct all instances of "sclera licterus" to "scleral
icterus."
Thank you for addressing these final issues carefully to ensure the manuscript meets publication
standards.
Best Regards,
Review for 10.1186/s12876-025-04008-5 (2025)

Title: Neonatal Intrahepatic Cholestasis Caused by Citrin Deficiency: Clinical Features, Genetic
Characteristics, and Treatment Outcomes
Version: 5 Date: 23 Apr 2025
Reviewer's report:
Thank you for the opportunity to review the revised version of the manuscript.
I believe the authors have adequately addressed the reviewers’ comments, and the manuscript
is now suitable for publication.
I have only one minor suggestion: in Table 1, the units for weight and height should be clearly
indicated (e.g., kg and cm).
Otherwise, I have no further comments.
Best regards,
Review for 10.1186/s12876-025-04008-5 (2025)

Title: Neonatal Intrahepatic Cholestasis Caused by Citrin Deficiency: Clinical Features, Genetic
Characteristics, and Treatment Outcomes
Version: 6 Date: 19 May 2025
Reviewer's report:
Thank you for addressing the previous comments and revising the manuscript accordingly. The
current version appears appropriate for publication. I have no further comments.
Best regards,
Review for 10.1186/s12876-025-04097-2 (2025)

Title: The Impact of Serum Neuregulin 4 (NRG#4) Levels on Non-Alcoholic Fatty Liver
Disease (NAFLD): A Systematic Review and Meta-Analysis
Version: 3 Date: 21 Mar 2025
Reviewer:  Ali Jafari
Reviewer's report:
Dear Authors,
I had the privilege of reviewing the article " The Impact of Serum Neuregulin 4 (NRG#4) Levels
on Non-Alcoholic Fatty Liver Disease (NAFLD): A Systematic Review and Meta-Analysis."
While the topic is highly relevant, the manuscript presents several methodological and linguistic
issues. I have substantial concerns regarding its current form and believe it is not suitable for
publication until these issues are comprehensively addressed. I commend the authors for their
valuable contribution and kindly request that they consider the following points:
1.  The search is outdated; please update it.
2. Why did you use JBI to assess the quality of the studies? What was the reason for not using
the Newcastle-Ottawa Scale?
3. It would be better to include demographic characteristics in the abstract.
4.  The introduction is a critical part of the manuscript, as it prepares the reader for the study's
topic. Consider revising it to enhance clarity and coherence.
5.   Why were other databases, such as WOS and proquest, not included in the search strategy?
6.   The manuscript should adhere to the PRISMA 2020 guidelines for reporting systematic
reviews. Figure 1 should be updated accordingly.
7.   The authors have reported results following the PRISMA checklist. Please provide a copy
of the PRISMA checklist (with page numbers indicated for each section) as a supplementary
appendix, as required.
8.   Have you considered including grey literature as a potential source of relevant studies?
9.   The data screening and selection process should include kappa statistics to assess inter-rater
agreement between authors.
10.   The discussion section is well-written and engaging. However, adding two additional
sections—"Clinical Implications" and "Future Directions"—could further enhance the study’s
impact.
11.   It would be better to list the studies in Table 1 chronologically by year.
12.   As per PRISMA guidelines, provide a table of excluded studies (those assessed in full text
but excluded for specific reasons) as a supplementary file.
13.   To ensure reproducibility, include the full electronic search strategy for all databases,
specifying any applied limits, as a supplementary file.
Review for 10.1186/s12876-025-04097-2 (2025)

Title: The Impact of Serum Neuregulin 4 (NRG#4) Levels on Non-Alcoholic Fatty Liver
Disease (NAFLD): A Systematic Review and Meta-Analysis
Version: 3 Date: 24 Mar 2025
Reviewer's report:
Dear editor,
Thank you for the opportunity to review your manuscript entitled "The Impact of Serum
Neuregulin 4 (NRG#4) Levels on Non-Alcoholic Fatty Liver Disease (NAFLD): A Systematic
Review and Meta-Analysis." This is a timely and important topic, and your effort in compiling
available evidence is appreciated. However, several issues need to be addressed to improve the
clarity, quality, and scientific rigor of your work.
General Comments:
The manuscript requires substantial language and grammar revision throughout. There are
numerous awkward phrasings and grammatical errors that affect the readability and clarity of
the paper.
Please update the global prevalence of NAFLD in the introduction.  The current value cited is
outdated. The most recent estimate is 30.2%, and this should be properly cited:
https://doi.org/10.1016/j.arcmed.2024.103043
Clinical Comments:
The role of Nrg4 as a clinical biomarker should be expanded upon. Discuss how it could
potentially be used for diagnosis, screening, or prognosis in real-world practice.
The authors should acknowledge the limited geographic diversity of the included studies (mainly
Asia and one from Europe), which may impact generalizability.
The phrase “Nrg4 has a protective effect” is used repeatedly. Please clarify whether this is a
correlation or causation based on the study design and findings.
The authors mention therapeutic implications briefly—this could be strengthened by discussing
how Nrg4 might be targeted in potential future treatments for NAFLD.
Statistical Comments:
The use of a fixed-effects model is inappropriate given the high heterogeneity (I² = 98.5%). A
random-effects model should be used, or the choice should be strongly justified.
Although meta-regression was performed, none of the findings were statistically significant (all
p > 0.05). These results should be presented as exploratory or hypothesis-generating.
The funnel plot and Egger’s test are mentioned, but the actual plots and p-values are missing.
Please include these in the results or as supplementary material.
The subgroup analysis by Nrg4 cutoff is helpful, but the rationale for selecting a 4 ng/ml cutoff
should be explained more clearly, supported by references or prior studies.
Review for 10.1186/s12876-025-04097-2 (2025)

Title: The Impact of Serum Neuregulin 4 (NRG#4) Levels on Non-Alcoholic Fatty Liver
Disease (NAFLD): A Systematic Review and Meta-Analysis
Version: 3 Date: 25 Mar 2025
Reviewer's report:
Thank you for the submitted manuscript. I have a few points that need to be addressed:
1. Since the systematic search was conducted in 2023, please update the search.
2. Please describe the search strategy for each database either in the main text or in the
supplementary materials.
3. In the data extraction section, there are explanations regarding unit conversions that should
be moved to the statistical analysis section.
4. In the statistical analysis section, the approach regarding potential publication bias has not
been mentioned.
5. The statistical analysis section lacks explanations for the choice of fixed-effects model instead
of random-effect model, as heterogenity is reported high in results.
6. In the results section, line 216 mentions that one of the studies was excluded due to a poor
effect size. Was a sensitivity analysis conducted for this exclusion?
7. The results of publication bias is not mentioned in the study.
8. The manuscript requires revision in terms of scientific writing.
Review for 10.1186/s12876-025-04097-2 (2025)

Title: The Impact of Serum Neuregulin 4 (NRG#4) Levels on Non-Alcoholic Fatty Liver
Disease (NAFLD): A Systematic Review and Meta-Analysis
Version: 4 Date: 11 May 2025
Reviewer:  Ali Jafari
Reviewer's report:
Thank you to the authors for addressing my comments thoroughly. All of my concerns have
been resolved.
The only remaining issue is with Figure 1. It is still in its previous format, and it needs to be
updated to the latest version of the PRISMA flow diagram.
Review for 10.1186/s12876-025-04103-7 (2025)

Title: Prognostic Value of the International Normalized Ratio to Albumin Ratio in Acute
Pancreatitis: Insights from MIMIC-IV Database
Version: 1 Date: 06 May 2025
Reviewer's report:
Question 1#Please point out the innovation of this article compared with other relevant studies.
Please point out the significance of this article.
Question 2#There are some editing and language errors in this article. Please review the entire
text and make corrections to make the expression more accurate.
Review for 10.1186/s12876-025-04103-7 (2025)

Title: Prognostic Value of the International Normalized Ratio to Albumin Ratio in Acute
Pancreatitis: Insights from MIMIC-IV Database
Version: 1 Date: 04 Jun 2025
Reviewer's report:
Fang et al. investigates the prognostic utility of PTAR (International Normalized Ratio to
Albumin Ratio) in predicting mortality among 459 ICU patients with acute pancreatitis (AP)
from the MIMIC-IV database. This study elevated PTAR independently predicted increased
all-cause mortality at 7, 14, 21, 28, 90, and 365 days post-admission, even after adjusting for
confounders (HRs: 2.31–4.91). Although the conclusion is interesting, there are some concerns
which should be addressed.
1. The analysis of PTAR’s performance across AP subtypes or severity grades are lacked.
2. Cutoff point and AUCs require external validation in independent cohorts.
3. Abstract states 456 patients were enrolled, Introduction/Methods state 459. This discrepancy
undermines data transparency and reproducibility.
4. No comparison to AP-specific scores is included, making clinical utility claims
unsubstantiated.
5.AP patients, especially survivors, may die from causes unrelated to AP. The study uses all-
cause mortality as the endpoint is not appropriate.
6. The conclusion that PTAR is "more precise" than alternatives is unsupported—it only matched
SOFA's AUC, not surpassed it.
Review for 10.1186/s12876-025-04103-7 (2025)

Title: Prognostic Value of the International Normalized Ratio to Albumin Ratio in Acute
Pancreatitis: Insights from MIMIC-IV Database
Version: 2 Date: 16 Jun 2025
Reviewer's report:
I highly appreciate the authors’ careful and sincere responses to the reviewers’ comments.
The revisions were well-considered and have significantly improved the manuscript’s clarity,
transparency, and methodological rigor.
One of the most commendable aspects of the revised manuscript is the authors’ effort to
conduct external validation of the PTAR cutoff value (0.58) using the eICU-CRD database.
This appropriately addresses potential overfitting concerns associated with deriving and testing
the threshold within the same cohort, and it strengthens the generalizability of the findings.
The consistent and statistically significant results across multiple models further support the
robustness of the proposed cutoff.
Additionally, the authors have clearly addressed my previous concerns regarding the restricted
cubic spline (RCS) analysis. They have specified the use of a Cox proportional hazards model
with three knots placed at the 10th, 50th, and 90th percentiles, and employed likelihood ratio
tests via the anova function in the rms package to assess both overall and nonlinear associations.
Their rationale for using the likelihood ratio test instead of the Wald test is statistically sound
and appropriate for the analysis conducted.
The revised Figure 4 is now well-annotated and clearly interpretable, and it aligns well with the
clinical narrative presented in the manuscript. Overall, the study now demonstrates improved
clarity, methodological transparency, and scientific validity.
I have no further suggestions. I recommend this manuscript for acceptance in its current form.
Review for 10.1186/s12876-025-03993-x (2025)

Title: Diagnosis model for gastric submucosal tumor based on multiple decision trees
comprising endoscopic and endoscopic ultrasonography features
Version: 0 Date: 29 Jul 2024
Reviewer's report:
I read with great interest the article titled “Diagnosis model for gastric submucosal tumor based
on multiple decision trees comprising endoscopic and endoscopic ultrasonography features” by
Shen Su et al. The authors have analysed 469 sub-epithelial lesions based on a hierarchical model
to aid in pre-operative decision making. I have the following comments to be made:
1. Introduction: line 46-47: authors need to correct the statement that diagnosis of SEL is by
EUS-FNA as majority studies, including recent meta-analysis have mentioned EUS-FNB to be
the procedure of choice (PMID: 37591258; PMID: 35264310). Mention the 2 studies as the
references.
2. Please provide the ethical committee number for the study.
3. Figure 1c: should mention decision model 2/3 to differentiate between GIST/schwannoma
versus lipoma; instead of only mentioning decision model 3.
4. The authors need to mention the figures 1,3-7 in the manuscript in the result section.
5. Table 1 does not show 13 variables, as highlighted by authors in results section. Please check
and rectify.
6. As per results section, those with p<0.001 were chosen as 13 variables: then as per results
of table 1 and 2, why wasn’t sex, age, mixed echo on EUS, submucosal level of origin, broad
based shape not chosen in the decision tree (all have p values <0.001). please clarify this aspect
in the manuscript.
7. Is it possible to combine figure 4-7 into a single line flow chart for better understanding?
Review for 10.1186/s12876-025-03993-x (2025)

Title: Diagnosis model for gastric submucosal tumor based on multiple decision trees
comprising endoscopic and endoscopic ultrasonography features
Version: 0 Date: 14 Oct 2024
Reviewer's report:
Dear authors,
I read with great interest your paper.
Regarding your manuscript, I believe the paper is well-written and clear in its aims. However,
it could benefit from revisions in both language and structure, and some typos need correction.
In particular, the Materials and Methods section requires a significant revision, as it is currently
difficult to understand and would benefit from simplification. There are some errors that should
be addressed (at least basing on my understanding of the work). Eg. on page 5, lines 95-98
are not clear to me. Additionally, on page 5, line 106, considering the phrase “If the latter, the
decision tree 3.4.5 determines” if I’m not wrong the decision tree 3 should not be included.
Furthermore, Decision Tree 2 is not included in the final algorithm (Figure 1c). I also suggest a
careful review of Figure 1c considering some mistakes I found.
Regarding the diagnostic model itself, I believe it is important to acknowledge the role of FNB
in the assessment of SELs that may require resection. FNB is not included in the algorithm. This
might explain why some benign lesions, such as lipomas and ectopic pancreas, were resected
in the study.
When considering the application of this work to clinical practice, it appears quite complex and
time-consuming. Evaluating 13 variables, applying separate decision trees for each pathological
type, and then completing the entire algorithm seems cumbersome. There are too many decision
points at each step. If Figure 1c represents the final algorithm to be used in clinical settings,
the number of questions that must be answered to achieve 75% overall accuracy is quite high.
I would suggest reducing the number or unifying some variables to make the process more
practical.
Another point to consider is that only six types of gastric SELs were included in the study. For
example, NETs were not part of the cohort. Additionally, since the patient cohort consists only
of those who underwent endoscopic resection, size should not be included in the algorithm due
to selection bias. Smaller lesions are often kept under surveillance, while larger ones may be
referred directly for surgery rather than endoscopic resection.
Review for 10.1186/s12876-025-03993-x (2025)

Title: Diagnosis model for gastric submucosal tumor based on multiple decision trees
comprising endoscopic and endoscopic ultrasonography features
Version: 0 Date: 25 Oct 2024
Reviewer's report:
Good work and too much effort.
But, the reader will find it difficult to digest and be sure that conclusions are sound and that the
final flow chart can be implemented in the real world.
Review for 10.1186/s12876-025-03993-x (2025)

Title: Diagnosis model for gastric submucosal tumor based on multiple decision trees
comprising endoscopic and endoscopic ultrasonography features
Version: 2 Date: 10 Jan 2025
Reviewer's report:
Thank you for addressing all my concerns in the revised manuscript. Your revisions have
significantly improved the clarity and overall quality of the work.
However, I would like to point out that, based on my understanding of the content and figure
captions, Figures 6 and 7 appear to be switched. Please review this to ensure the figures are
correctly labeled.
Once this minor issue is addressed, I believe the manuscript will be ready for publication. Thank
you for your efforts in responding to the feedback.
Review for 10.1186/s12876-025-04055-y (2025)

Title: The prognostic value of Immunoscore in the early-onset colorectal cancer
Version: 1 Date: 01 Mar 2025
Reviewer's report:
Review
This study establishes a Chinese population-specific Immunoscore (IS) framework through
neural network-based quantification of CD3+/CD8+ tumor-infiltrating lymphocytes and
validates its prognostic significance in early-onset colorectal cancer (EOCRC). The results
demonstrate that IS effectively stratifies EOCRC patients by recurrence and metastasis risks,
independent of TNM staging. As EOCRC represents a rare but epidemiologically significant
subgroup with rising global incidence and aggressive clinicopathological features, this work fills
a critical knowledge gap by providing the first evidence of IS applicability in this underserved
population. By bridging the gap between immune profiling and precision oncology in EOCRC,
this work provides foundational insights with significant clinical translation potential, offering
actionable insights to guide postoperative surveillance and adjuvant therapy decisions.
Several revisions should be made:
1.The term “nCRT” in 190 and “CMOR” in line 192 were not defined clearly.
2.The word "unsing" in line 142 may be incorrect, please check the spell.
3.It is recommended to shorten and simplify the introduction section appropriately.
Overall Assessment
Overall, this study demonstrates the prognostic value of IS in early-onset colorectal cancer using
a neural network model. Acceptance for publication is recommended with minor revisions.
Review for 10.1186/s12876-025-04055-y (2025)

Title: The prognostic value of Immunoscore in the early-onset colorectal cancer
Version: 1 Date: 03 Mar 2025
Reviewer's report:
The authors' study is well thought out and methodologically rigorous, but the sample size is
somewhat pitifully small for a prognostic model, with only 36 cases. In addition, there should be
many studies that have been developed for prognostic models for early-onset colorectal cancer,
and I hope that the authors can present other people's studies and compare them in the discussion.
Other than that, I have no other suggestions.
Review for 10.1186/s12876-025-04055-y (2025)

Title: The prognostic value of Immunoscore in the early-onset colorectal cancer
Version: 3 Date: 15 May 2025
Reviewer's report:
The authors have thoroughly addressed the reviewers’ comments and provided detailed
clarifications where necessary. The revisions have improved the clarity and scientific rigor of
the manuscript. I recommend that the paper be accepted for publication.
Review for 10.1186/s12876-025-04114-4 (2025)

Title: IgG4-related cholangitis – distinguishing from other benign biliary strictures: clinical
features, imaging, and response to treatment: a retrospective study
Version: 1 Date: 07 May 2025
Reviewer's report:
The author describes the bile duct wall thickening in IgG4-related cholangitis (IgG4-
RC) as "symmetrical," but since the thickening is generally circumferential, a term like
"circumferential" would be more appropriate.
Review for 10.1186/s12876-025-04114-4 (2025)

Title: IgG4-related cholangitis – distinguishing from other benign biliary strictures: clinical
features, imaging, and response to treatment: a retrospective study
Version: 1 Date: 20 May 2025
Reviewer:  Nabeel Azeem
Reviewer's report:
It would be helpful if the authors could clarify/be more specific on how they identified the patient
population prior to chart review. Did they do a keyword search of an electronic medical record to
identify all biliary strictures, or were billing codes used, or was there a prospectively maintained
list of patients with biliary strictures.
Was EUS utilized for sampling of any adjacent lymphadenopathy?
I would disagree with the definition given for ‘Indeterminate biliary stricture’. These are
strictures where the initial work up failed to determine an aetiology but statistically most of them
are malignant. Therefore, many of these would not remain stable over time. The ones that did
remain stable by definition were benign. This is more clear in the flow chart but the definition
should be changed.
What modality was used to determine the thickness of the bile duct? EUS/MRCP/CT? There
will likely be between modality difference even in the same patient.
“However, patients with IRC tended to be older, with a mean age of 65 years, compared to 58.5
years in those with other BBS (p=0.085)” This comparison did not reach statistical significance
and therefore there is no difference in age between the two groups.
Using the data you already have, it would be useful to report sensitivity and specificity of
elevated IgG4 in IRC compared to the rest of the BBS cohort. ROC curve could then be generated
to understand what IgG4 cut off would be useful.
How were the length of the strictures determined? On MRCP or ERCP? As reported at the time
of procedure/imaging or measured post-hoc?
Why was there any response to steroids in the BBS group (10.5%)? If they responded to steroids,
wouldn’t they be in the IRC group/have IgG4-cholangiopathy?
“Among the other BBS groups, the aetiologies included stone-induced bile duct stricture (37%),
indeterminate biliary strictures (18%), chronic pancreatitis (18%), and other BBS (25%).” ---
Indeterminate biliary stricture is not an aetiology. By definition, it means we do not know what
the etiology is.
“Additionally, the incidence of ascending cholangitis was significantly lower in the IRC group
compared with the other BBS groups (15.8% vs. 66.7%; p < 0.001) in our study.”--- Shouldn’t
this be 15.8% vs 45.3% according to table 1?
Review for 10.1186/s12876-025-04114-4 (2025)

Title: IgG4-related cholangitis – distinguishing from other benign biliary strictures: clinical
features, imaging, and response to treatment: a retrospective study
Version: 2 Date: 20 Jun 2025
Reviewer's report:
The authors have responded to comments from reviewers appropriately. This manuscript has
been well revised according the reviewer's comments.
Review for 10.1186/s12876-025-04114-4 (2025)

Title: IgG4-related cholangitis – distinguishing from other benign biliary strictures: clinical
features, imaging, and response to treatment: a retrospective study
Version: 2 Date: 22 Jun 2025
Reviewer's report:
The manuscript has been thoroughly revised, and I have no further comments at this time.
Review for 10.1186/s12876-025-04106-4 (2025)

Title: Features of defecation dysfunction among patients with Hirschsprung disease in early
childhood
Version: 1 Date: 13 Aug 2024
Reviewer:  John Gillick
Reviewer's report:
Clear, well constructed study with good sample size.  The conclusions seem robust and clinically
relevant.
There are two corrections I would suggest
1. Methods  line 17-"such as spending bowel management for a few days"-do you mean
suspending?
2. Discussion-section 4.2-"the inability to tolerate defecation"-do you mean initiate? Please
clarify.
Review for 10.1186/s12876-025-04106-4 (2025)

Title: Features of defecation dysfunction among patients with Hirschsprung disease in early
childhood
Version: 1 Date: 27 Aug 2024
Reviewer's report:
Review of the manuscript ” Features of defecation dysfunction among patients with
Hirschsprung disease in early childhood”. This is a cross-sectional study of the bowel function
after surgery for Hirschsprung’s disease assessed with Bowel Function Score in 204 children
with Hirschsprung’s disease compared to 156 healthy children at a single center. The study
shows, as expected that children with Hirschsprung’s disease have worse bowel function
outcome compared to healthy children. This is an impressive cohort and it is very much
appreciative that the authors chose a validated questionnaire for assessing bowel function. With
regards to this, there are some comments and questions to the authors.
1. How was the patients and healthy controls recruited? The authors must explain how these
individuals were selected and the response rate among the healthy controls. This is of importance
for the reader to evaluate the quality of the study.
2. Is the Bowel Function Score translated and validated in Mandarin? Could the authors explain
if the questionnaire already has been translated?
3. Usually the affected parts in patients with Hirschsprung’s disease in divided into recto-
sigmoid, long segment and total colonic aganglionosis, why did the authors show their
categories?
4. Since the result is presented in Table 1-4, the results can be shortened with the data already
presented in the different Tables.
5. For the results, I miss a Table 1 showing the baseline data as age, sex, level of aganglionosis,
etc. This Table is of importance to be able to interpret the results even though the authors have
stated that there was no difference been the groups.
6. How were these individuals operated on? Terp and lap terp? Even AIHD?
7. I think that the authors should highlight the social problems more, since these are important
issues that can affect the individual a lot.
Review for 10.1186/s12876-025-04106-4 (2025)

Title: Features of defecation dysfunction among patients with Hirschsprung disease in early
childhood
Version: 1 Date: 20 Oct 2024
Reviewer:  Alessio Pini Prato
Reviewer's report:
The paper is intriguing but I have some concerns
English form should be improved throughout the text.
Materials and Methods
1) there are no statements regarding the power analysis performed to determine the number of
patients and controls. Even if no power analysis was done, this should be mentioned in the text.
2) No mention is done regarding the age and sex matching of cases and controls and if present
or not this aspect should be addressed
Results
3) It  is unclear to me the meaning of the following sentence: “ In our study healthy control
children who were < 3 years of age had completed toilet training”
4) It is unclear the population of HSCR we are dealing with. the sentence stating: “There was
no difference between patients with RSHD and healthy control children with respect to the
male:female ratio, age, and weight at follow-up (all, P>0.05)”  suggest a distorced epidemiology
in this series of patients. In fact, I would expect a dramatic male prepondrance  with a statistically
significant differences of male to female ratio when comparing rectosigmoid HSCR and healty
population. Even comparing rectosigmoid, long and ultra long J HSCR, we should observe
a 4/5:1 ratio in classic form decreasing to a nearly 1:1 ratio in total colonic or extended
aganglionosis. This aspect should be considered for a better rephrasing of results section or to
develop an adequate discussion.
5) the statement “ These findings indicated that an inadequate ability to feel or report the urge
to defecate occurred in all HD types and was more severe in DTHDs and AIHDs, which may be
attributed to damage from intact sensations. The intact sensation lies on the anal tract or dentate
line and can be damaged during PT surgery by a lower level of dissection or anastomosis at the
dentate line [31]” is a clear discussion of the results and it should be moved to  the appropriate
section. This issue, inappropriate location of sentences discussing results is repeated throughout
the Results section and should be heavily revised.
Discussion
6) This section is nicely presented but should include a number of statements addressed in the
results section as mentioned above.
All in all this paper is nice but should be revised according to reviewer concerns in order to be
considered for publication.
Review for 10.1186/s12876-025-04109-1 (2025)

Title: Metabolic Dysfunction, Cirrhosis, and HCV Genotype 3a Drive Type 2 Diabetes Risk in
Chronic Hepatitis C: A Southern Chinese Cohort Study
Version: 3 Date: 02 Jun 2025
Reviewer's report:
The study addresses the increasingly recognized extrahepatic manifestations of HCV infection,
particularly T2DM, and its clinical risk factors. Regarding study design, multivariate logistic
regression enhances causal inferences, while the 1:1 matched case-control approach lessens
confounding. The materials and methods are well structured, and the results can be easily
tracked.
On the other hand, there are consistent problems in punctuation, grammar, and word choice
that make the text difficult to read. Also, in the results section, HOMA-IR has an OR < 1 in
multivariate analysis, indicating a protective effect that defies previous research and clinical
expectations. It is necessary to explain this disparity. Genotyping was only performed on
44 patients with CHC+T2DM, which may not provide robust statistical power for subgroup
analysis. I suggest adding to limitations. The discussion is repetitive and could be condensed.
Several paragraphs reiterate previous findings without adding new interpretation.
Finally, I observed that the manuscript alternates between “HCH” and “CHC,” “T2DM” and
diabetes. It is necessary to use consistent terminology all throughout.
Review for 10.1186/s12876-025-04109-1 (2025)

Title: Metabolic Dysfunction, Cirrhosis, and HCV Genotype 3a Drive Type 2 Diabetes Risk in
Chronic Hepatitis C: A Southern Chinese Cohort Study
Version: 4 Date: 21 Jun 2025
Reviewer's report:
I believe that the changes I requested were successfully made.
Review for 10.1186/s12876-025-04096-3 (2025)

Title: Intestinal microbiota in adults with cholangiocarcinoma identifies the dysregulated
Blautia species and bile acid metabolic pathways
Version: 2 Date: 23 May 2025
Reviewer's report:
Review comments:
1. In the abstract, line 30, sentences are repeated. They give a similar meaning of line 24
2. Lines 45 & 46 remove unnecessary hyphens
3.  Line 50 & 116Check reference format and size.
4. Sample size is relatively small, and a regionally homogenous cohort may limit
generalizability.
5. Give justification for the sample collection time.
6. How DNA concentration and purity was checked, give clear methodology for that.
7. Check the all references format and size
8. Check the sentence in line 166, you mentioned 51 CCA patients, but in the methodology you
pointed out 29 healthy individual  and 23 CCA sample. Clarify that.
9. Line 263, the KEGG abbreviations are repeated
10. The methods mention using ROC and DCA for model evaluation, but these are not included
in the figures or results section.
11. OTU terminology is outdated for WGS data. Replace with MAG, species bin, or
metagenomic contigs.
12. The term “Blautia streptococcus spp.” is not taxonomically valid. Revise taxonomy
references. Ensure species-level assignments are based on accepted thresholds.
13.  The connection between reduced Blautia and decreased bile acid metabolism is plausible
but hypothetical. Acknowledge the limitation and propose validation (e.g., qPCR of metabolic
genes, butyrate measurement, or animal studies).