JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-03937-5 (2025)

Title: M64HCl, a focal adhesion kinase activator, promotes intestinal mucosal healing in rats
Version: 0 Date: 02 Aug 2024
Reviewer's report:
I do not support the publication of this manuscript. In this article, the authors aim to identify
if M64HCl treatment in rats with intestinal injury (induced by 75% acetic acid) can promote
intestinal healing (effects that are observed in mice). Here, the authors claim to observe an
improvement in ulcer area, pFAK immunoreactivity and alleviation of intestinal pathology.
First, we do not know the extent to which intestinal injury is established in the basic model
in the rats, as this has not been described sufficiently especially in this rat model (i.e., clinical
scoring signs, cytokine profiles, weight change, survival, etc.). The authors refer to “pathological
factors” as causes for mucosal injury but no pathogens were tested thus overstating the relevance
of their findings. The data presented by the authors is also very weak and does not accurately
represent what the authors are claiming to be true. Although the authors show that there is a
reduction in ulcer area in figure 1 (where C and D are repeats), the evidence for improvement
in intestinal pathology and FAK activation is limited (H&E and immunohistochemistry do not
capture what the authors claim to be the case -> the images are very weak, staining issues, etc.).
For example, the authors claim things like increased inflammatory cells but the provided images
do not capture this. These 3 figures plus a table are the only results provided but this is very
weak evidence.
Review for 10.1186/s12876-025-03937-5 (2025)

Title: M64HCl, a focal adhesion kinase activator, promotes intestinal mucosal healing in rats
Version: 0 Date: 07 Aug 2024
Reviewer's report:
Manuscript is well written. Methods are sound and discussion highlights interesting and relevant
points for future investigations of M64HCl.
If possible, I would like to see in this manuscript the addition of ulcer scoring using the stated
pathological features in the histological analysis as well as quantifying the IHC of p-FAK.
It would be interesting to see, in the future, studies focusing on the mechanism of action of
M64HCl through the FAK-Src complex in this in vivo model, to support previous publications
in vitro.
Review for 10.1186/s12876-025-03937-5 (2025)

Title: M64HCl, a focal adhesion kinase activator, promotes intestinal mucosal healing in rats
Version: 2 Date: 06 Mar 2025
Reviewer's report:
The authors conducted further analyses as reviewers requested and responded well to additional
questions providing references, etc. Before final submission, I would like to also see authors
clarify in the figures which experimental group is which instead of just describing Figure A
refers to control, for example. Titles above each picture will be much clearer for the reader.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 0 Date: 29 Oct 2024
Reviewer's report:
This study explored the risk factors of colon cancer lymph node metastasis, and established
a prediction model based on these factors. The study has certain clinical significance, but the
following problems still need to be solved to make the study more clinical popularization.
(1) The sample size of the study is too small, so it is suggested to use public databases such as
SEER database to expand the sample size for modeling;
(2) The study did not carry out validation of external data sets, which is very important for the
effectiveness evaluation of the model, and it is suggested to supplement the results in this respect;
(3) I do not see the innovativeness of this study compared with other similar studies, please
elaborate.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 0 Date: 15 Nov 2024
Reviewer's report:
Title “Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data”
Thank you for the opportunity to review this article. I have the following comments.
This study presented a novel nomogram to predict the risk of lymph node metastasis in colon
cancer patients.
This study will make certain contributions to the field of research on the prediction model of
lymph node metastasis in colorectal cancer patients. However, some points should be addressed.
“Major issues”
1) Generally, the derivation cohort and validation cohort are required to build a nomogram; in
the absence of a cohort for external validation, it is common practice to split the total cohort.
2) Although lymph node status on CT is a crucial factor in this nomogram (nearly 90 points),
there is no description of what findings resulted in a positive lymph node diagnosis by CT.
3) Intestinal obstruction is also not defined. This is also a crucial factor in this nomogram (100
points) and should be defined.
4) The clinical significance of this nomogram needs to be more specifically described. If
this nomogram indicated that a patient is likely to be positive for lymph node metastases
preoperatively, what difference in decision-making would be made in clinical practice?
“Minor issues”
1) The “CIC” in the abstract should not be abbreviated.
2) Regarding lines 18-21 of the Introduction section, the authors mentioned that accurate
preoperative prediction of regional lymph node metastasis facilitates postoperative adjuvant
chemotherapy, but postoperative chemotherapy is based on postoperative pathology results. The
authors should correct this description to be accurate.
3) One unique aspect of this nomogram is that it includes blood type as a factor. However, the
percentage of blood types is known to vary considerably around the world. It is unclear whether
it has external validity for cohorts in other countries.
4) In table 2, it should be clarified what is the reference value of age.
5) RAS, BRAF, and MSI status may be also an important predictive factor, and this information
should be provided.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 0 Date: 17 Nov 2024
Reviewer's report:
This article discusses a study on predicting the risk of lymph node metastasis (LNM) in colon
cancer (CC) patients. The research team developed and validated an online dynamic nomogram
based on preoperative data to estimate the risk of LNM in colorectal cancer patients, which
performed well overall. However, there are several limitations:
1. Although the model performs well in internal validation, external validation is essential to
assess its applicability and robustness in different populations or datasets. Without it, the model’s
generalizability and potential for wider application are limited.
2. The article does not thoroughly explain the quality control measures during data collection
and processing, such as data cleaning and handling of outliers. These details are crucial for
evaluating the reliability of the data and the credibility of the study results.
3. The study design and discussion of results do not sufficiently address potential biases, such as
selection bias, information bias, or confounding factors. A deeper analysis of these limitations
would help readers understand the results more comprehensively and provide direction for future
improvements.
4. Language and grammar issues:
i#Abbreviations (e.g., LNM, CT, ROC) should be spelled out the first time they appear with the
abbreviation in parentheses. This standard is not consistently followed, potentially confusing
readers unfamiliar with the terms.
ii#Some sentences are long and complex, which may hinder readability. For example: "The
Least Absolute Shrinkage and Selection Operator (LASSO) method was used to initially
screen predictors from 21 variables to better deal with the problem of model overfitting and
multicollinearity associated with high-dimensional samples."
iii: There are instances of unnecessary repetition. For example, "The nomogram was developed
to predict the risk of LNM in colon cancer patients. The nomogram is a tool that helps predict
the risk of LNM in colon cancer patients." Repetition should be avoided.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 1 Date: 19 Dec 2024
Reviewer's report:
The author's response to the review comments is comprehensive and constructive. They have
made significant revisions and additions to address the issues and concerns previously raised.
These modifications have enhanced the quality and credibility of the research, making the
paper more polished and ready for publication. I recommend acceptance for publication in your
journal.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 1 Date: 17 Jan 2025
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses a testable research
question(s) (brief or other article types: is there a clear objective)?
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with technical rigor to allow
confidence in the results?
No - there are minor issues
STATISTICS - Is the use of statistics in the manuscript appropriate?
Not sure - I am not able to assess the statistics in this study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Is the current version of this work technically
sound? If not, can revisions be made to make the work technically sound?
Maybe - with major revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: dear authors
I read with great interest your research paper about the prediction of LNM in colon cancer.
This is a quite interesting topic since we are facing a new era of oncological treatment with
an imminent possibility of neoadjuvant treatment also in colonic cancer. The importance of
predicting advanced stages is therefore clear and it should be stressed in the paper.
Some comments:
- please reduce the length of the manuscript to less than 3000 words. The abstract to 250 (is too
long and detailed in methods!). Please focus the introduction on the topic.
- radiological images should be reviewed by a blinded dedicated radiologist in order to assess
the real predictive value of CT scan.
- the main limitation of the study is the relatively small number of patients included (300 patients
for such a common disease is a very small number). please mention it in the limitation section
- statistical method adopted is really very complex and it should be revised by a statistical editor.
REQUESTED REVISIONS:
please see my comments above
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 2 Date: 14 Feb 2025
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
No - there are minor issues
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
No - there are major issues
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
No - there are major issues
STATISTICS - Is the use of statistics in the manuscript appropriate?
Not sure - I am not able to assess the statistics in this study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
No - there are major issues
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
No - manuscript has some fundamental flaw(s)
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: Dear authors
Suggested modifications are lacking. The paper seems the same of the previous time. It's still
too long and too detailed in section without any interest for the reader.
Moreover the real evidence derived from such a small number of patients is really vey
questionable.
Please see and follow previous suggestions
REQUESTED REVISIONS:
see my comments above
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 2 Date: 14 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-While the introduction discusses various factors (e.g., symptoms, tumor markers), it would
benefit from specifying some of the key clinical or laboratory factors that are anticipated to be
significant in the prediction of LNM, offering a clearer view of the model's predictors.
The introduction generalizes some points about CRC research but does not provide specific
examples of studies that might have successfully addressed LNM prediction or those that fell
short, which could help contextualize the gap more specifically.
-Although excluding patients with missing data or high missing rates is reasonable, this approach
might lead to selection bias. It would be beneficial to explore if a sensitivity analysis or
alternative methods like multiple imputation could be used to mitigate potential biases arising
from missing data.
-While the use of LASSO helps mitigate overfitting, the large number of variables being
considered might still introduce complexity. Some justification of why all 21 variables are
necessary (and how each contributes to model performance) would enhance transparency.
The study includes endoscopic data as a predictor, but there is limited information on how
endoscopic findings are specifically incorporated into the model. Clarifying this could help
readers better understand the role of this factor.
-You clearly highlight the clinical importance of preoperative prediction for LNM, especially
in colon cancer (CC). Perhaps, a brief comparison with other existing tools/models for LNM
prediction would further emphasize the novelty and advantage of your model. For example,
you could mention if the nomogram's performance is significantly better than commonly used
clinical tools, such as the TNM staging system, in terms of accuracy, usability, or clinical utility.
-You speculated that tumor ulcers are correlated with increased LNM in CC patients, but also
mentioned that the exact mechanism remains unclear. Expanding this hypothesis could make
the discussion even more insightful. You could mention the potential biological or molecular
mechanisms underlying this association, or discuss studies in other cancers that have explored
how ulceration might promote lymph node metastasis (e.g., through inflammation or tumor-
induced immune suppression). This could pave the way for future studies examining the biology
of LNM in CC.
Review for 10.1186/s12876-025-03958-0 (2025)

Title: Predicting the risk of lymph node metastasis in colon cancer: development and validation
of an online dynamic nomogram based on multiple preoperative data
Version: 3 Date: 17 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03949-1 (2025)

Title: The Prognostic Value of AST-Lymphocyte Ratio Index in Liver Cancer Patients Treated
with TACE: A Systematic Review and Single-Center Retrospective Study
Version: 1 Date: 20 Feb 2025
Reviewer's report:
In revised manuscript,  Line  62  GLOBOCAN 2018 is outdated, the latest one is GLOBOCAN
2022
Reference #3 and #6 are the same.
Line 168   Neutrophil Lymphocyte ratio is a ratio, with no unit.
Fig 7 is  not the best way to present data . Consider excluding outliers and consider why outliers
exist.
Fig 8 cannot stand independent from the text.  Provide survival numbers at each time point below
X axis, provide p value in the figure.
The discussion part is too  wordy and repetitive on the same point, for example , Line 248-262.
Overall, this manuscript consists of two separate studies (one meta-analysis , the other
retrospective study) . The retrospective study did not add much value on the top of meta-analysis.
Instead of solving the issue of various ALRI cutoffs among  the prior studies,  the retrospective
study just introduced a new cutoff without reconcile the difference.  Consider splitting this
manuscript into two.     As a systemic review and meta-analysis, there are  many angles you can
expand the discussion, such as, comparing other studies in other biomarkers broadly, compare
different  indications, and so on.     So is the retrospective analysis .    However, the discussion
part of present manuscript  is weak and repetitive.
Review for 10.1186/s12876-025-03949-1 (2025)

Title: The Prognostic Value of AST-Lymphocyte Ratio Index in Liver Cancer Patients Treated
with TACE: A Systematic Review and Single-Center Retrospective Study
Version: 2 Date: 12 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03949-1 (2025)

Title: The Prognostic Value of AST-Lymphocyte Ratio Index in Liver Cancer Patients Treated
with TACE: A Systematic Review and Single-Center Retrospective Study
Version: 2 Date: 25 Mar 2025
Reviewer's report:
The two separate components of this manuscript  are
a meta-analysis of prior studies and a single-institution retrospective study. The retrospective
study
Given various ALRI cutoffs among the prior studies, meta-analysis didn't  attempt to investigate
deeper to  reconcile the nuance and provide a pooled cutoff (think of methods like the bivariate
random-effects model ).  Hence,  there's no contribution to adding any new evidence to the
published data.
The retrospective clinical study introduced a new cutoff without reconcile the
difference from the prior studies, either.  There's perhaps baseline characteristics difference
between author's cohort and historical data. (The cutoff is much lower than the majority of
cutoffs from other articles, except Zheng's ) .  There's a great need to explain this.  What's more,
tumor size and number are all independently predictive of OS,  which means ALRI does not
count tumor burden itself.  There's a great interest to add tumor factor into the prediction model.
Lastly, this retrospective analysis is only based on 127 cases , which are much less than other
studies. Unless the population is significantly different from other studies,  very limited value
is added to existing literature.
The manuscript needs grammar check and proofreading before resubmission
Review for 10.1186/s12876-025-03949-1 (2025)

Title: The Prognostic Value of AST-Lymphocyte Ratio Index in Liver Cancer Patients Treated
with TACE: A Systematic Review and Single-Center Retrospective Study
Version: 3 Date: 07 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03943-7 (2025)

Title: Trajectories of depressive symptoms and risk of chronic liver disease: Evidence from
CHARLS
Version: 1 Date: 19 Feb 2025
Reviewer's report:
The manuscript does not provide a theoretical framework to justify the selection of variables.
The rationale behind including specific variables is unclear. You are testing here and why.
The description of the subgroup analysis is overly vague. The manuscript mentions the use
of RERI, AP, and SI to evaluate additive interaction, but the results section only provides a
brief statement without clear explanation of the values or their implications. Additionally, the
concept of multiplicative interaction is mentioned without proper context or detailed results.
Please provide a more comprehensive explanation of how these measures were calculated and
their interpretations, and ensure that the corresponding data in the tables are clearly described.
For instance, the statement regarding the association between depressive symptom trajectories
and the risk of CLD in almost all subgroups (Table 3) and the absence of interactions
(Table 4) lacks sufficient detail. It is recommended to consult established  (DOI: 10.1186/
s13195-020-00691-6) to ensure that subgroup analyses are reported comprehensively, including
clear definitions, appropriate interaction tests, effect sizes, confidence intervals, and P-values
for interactions.
The manuscript does not clearly indicate whether the results presented are weighted or
unweighted. Please clarify the weighting method applied in the analysis and ensure that the
appropriate weights are used to account for the sampling design if necessary.
Add expert assessments of the results obtained.
Review for 10.1186/s12876-025-03943-7 (2025)

Title: Trajectories of depressive symptoms and risk of chronic liver disease: Evidence from
CHARLS
Version: 1 Date: 26 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The exclusion of participants with psychiatric disorders (4798) and pre-existing CLD (1050)
in the initial waves is understandable to avoid confounding. However, it would be useful to
elaborate on whether this exclusion might introduce any bias into the results. For example,
excluding those with psychiatric disorders may miss individuals with comorbid depression and
liver disease, which could affect the generalizability of the findings.
-While the study mentions that CLD is diagnosed by a physician and self-reported by
participants, the method of diagnosis (e.g., clinical examination, biomarkers, medical records)
could be better described. Without more details on how CLD was diagnosed, the accuracy of
the CLD classification may be questioned. It would be ideal to specify whether the diagnosis
was confirmed by a medical professional at each wave or if self-reported data alone were used.
-The exclusion of participants with incomplete data (e.g., missing CES-D scores or CLD
data) raises the question of whether missing data might introduce bias. It would be helpful to
clarify the approach used for handling missing data, such as whether imputation methods were
employed or if a complete case analysis was conducted. This would address concerns about the
representativeness of the study sample.
-While LCGM and GMM are excellent statistical approaches to analyzing longitudinal
depressive trajectories, it might be beneficial to explain why these specific methods were chosen
over other possible techniques, such as latent trajectory models or other growth mixture models.
Additionally, more details on how the model fit was assessed (e.g., fit indices, cross-validation)
would help readers understand the robustness of the model selection process.
-The study excludes cancers from the CLD category, but it would be valuable to explain why
this exclusion was made. It would also be useful to specify how the diagnosis of CLD was
handled in the presence of comorbid conditions like cancer or other liver-related diseases that
might complicate the analysis.
-The authors acknowledge that they did not explore the bidirectional relationship between
depressive symptoms and CLD. Depression could both be a cause and a consequence of CLD,
and this aspect should be addressed to fully understand the dynamics of the relationship. The
lack of consideration of this bi-directionality is a significant limitation.
-While the study adjusts for confounders, there could be other unmeasured variables (e.g.,
genetic factors, access to healthcare, or socioeconomic status) that might influence both
depressive symptoms and CLD risk. Addressing these potential confounders would provide a
clearer understanding of the relationship between the two.
Review for 10.1186/s12876-025-03959-z (2025)

Title: Preoperative immune prognostic index predicts the prognosis and postoperative adjuvant
chemotherapy benefits of esophageal squamous cell carcinoma after minimally invasive
esophagectomy
Version: 2 Date: 23 Mar 2025
Reviewer's report:
This study categorized patients with esophageal squamous cell carcinoma (ESCC) who
underwent minimally invasive esophagectomy (MIE) into two groups: a low IPI group and a
high IPI group. It explored the relationship between these groups and their prognosis. The low
IPI group showed significantly better overall survival (OS) and disease-free survival (DFS) than
the high IPI group. Additionally, a subgroup analysis revealed that patients in the high IPI group
who received adjuvant chemotherapy (AC) had a better prognosis than those who did not receive
it. In other words, the authors suggest that patients with a high IPI will likely benefit from AC.
While the study presents interesting findings, the authors must address some issues.
1.
Analyses by a co-author specializing in statistics would improve the manuscript.
2.
What is the standard therapy for patients with locally advanced esophageal squamous cell
carcinoma (ESCC) in the author's hospital or country? Why were these patients excluded from
receiving preoperative neoadjuvant chemotherapy or chemoradiotherapy?
3.
The methods section should provide detailed postoperative chemotherapy protocols and explain
the treatment's indications.
4.
The methods section should outline the surgical procedures (McKeown and Ivor-Lewis).
5.
Overall Survival (OS) includes deaths from causes other than ESCC. To better understand the
relationship between IPI and the prognosis of ESCC patients, I request that the authors include
the analysis results for Disease-Specific Survival (DSS) and discuss the results.
Review for 10.1186/s12876-025-03897-w (2025)

Title: Diagnostic challenges of inflammatory submucosal tumor-like lesions: a multicenter
propensity score- matching analysis
Version: 2 Date: 11 Apr 2025
Reviewer:  Mohamed H. Zidan
Reviewer's report:
Dear Authors,
Re: Diagnostic challenges of inflammatory submucosal tumor-like lesions: a multicenter
propensity score-matching analysis
Thank you for submitting the revised version of your manuscript and addressing the points
raised in the initial round of peer review. I have carefully reviewed your responses, the
updated manuscript, figures, tables, and supplementary materials. Overall, your revisions
have significantly improved the manuscript's clarity, methodological transparency, and clinical
relevance. The study provides a valuable contribution to the literature on diagnostic strategies
for inflammatory submucosal tumor-like lesions (I-SMTLs), a rarely addressed yet clinically
important subset of submucosal lesions.
You have satisfactorily addressed all seven major concerns from the first-round review. your
manuscript presents a rigorous multicenter analysis with important clinical implications for the
diagnosis and management of I-SMTLs.  All previous concerns have been appropriately and
comprehensively addressed.
Thank you
Review for 10.1186/s12876-025-03945-5 (2025)

Title: Unraveling the Site-Specific Features in Small Intestinal Stromal Tumors: A
Retrospective Study
Version: 2 Date: 04 Mar 2025
Reviewer:  Ryosuke Sato
Reviewer's report:
Thank you for allowing me to review this thoroughly researched paper on small intestinal GISTs.
This is a retrospective study to enhance the understanding of the clinical characteristics and
disease behavior of small intestinal GISTs based on their sites.  Following are my comments
for this manuscript.
Introduction:
In previous studies, small intestinal GIST exhibited a higher rate of lymph node metastasis
compared to gastric GISTs, however, only one case showed lymph node metastasis in this study.
Reference #8 also stated that the lymph node metastasis rate for small intestine GIST was around
10%, but what is the cause of this difference?
Methods:
Patients who were diagnosed as GIST based on immunohistochemical findings were included in
this study.  Patients who were diagnosed as GIST based on immunohistochemical findings were
included in this study. What was the immunohistochemical profiling of these patients? Were all
patients positive for c-kit? Was anyone positive for CD-34 or DOG-1?
Results:
Tumor rupture is the major symptom affecting the prognosis of patients with GISTs. Did anyone
undergo emergency surgery because of tumor rupture?
What led to the patient being diagnosed with GISTs, and what was the modality used for
diagnosing, for example, CT, MRI, EGD, balloon-assisted enteroscopy, capsule endoscopy, or
abdominal US?
Patients for familial GIST or neurofibromatosis type 1 often present multiple GISTs. Was
anyone with a hereditary disease in this study? Any multiple GISTs?
Discussion:
You mentioned, "The higher rate of bleeding in the jejunum is likely because it has the richest
blood supply in the small intestine.". Please provide references.
It seems that the tumor characteristics of jejunal GISTs and ileal GISTs are almost the same.
Please summarize in an easy-to-understand way the reasons why it is better to distinguish
between them and when to suspect them based on the symptoms that appear.
Review for 10.1186/s12876-025-03945-5 (2025)

Title: Unraveling the Site-Specific Features in Small Intestinal Stromal Tumors: A
Retrospective Study
Version: 2 Date: 06 Mar 2025
Reviewer's report:
Overall, while the study is descriptive, it examines a large number of small intestinal GIST
cases and provides valuable insights that could serve as a reference for clinical practice.
The manuscript is generally well-structured and informative. To further enhance clarity and
readability, I suggest considering the following revisions:
1. I noticed that the limitations of the study are explicitly mentioned within the results section
of the abstract. Typically, limitations are discussed in the "Discussion" section rather than the
abstract, as the abstract is intended to provide a concise summary of the study’s objectives,
methods, key findings, and conclusions. To improve readability and maintain the conventional
structure, I suggest either REMOVING THE MENTION of study limitations from the abstract
or rephrasing it more concisely. For example, instead of:
"These findings necessitate subsequent verification through prospective multicenter studies to
address the inherent limitations of the retrospective single-center design, particularly regarding
selection bias and generalizability constraints."
You could consider a more succinct statement, such as:
"These findings warrant further validation in prospective multicenter studies."
This adjustment would help maintain a clear and focused abstract while ensuring that the study's
limitations are appropriately addressed in the discussion section.
2. The authors state, "Therefore, the purpose of this study is to thoroughly elaborate the clinical
features and biological behavior of small intestinal GISTs at different sites, with the hope of
aiding the diagnosis and treatment of this unusual and less characterized disease." and "We
documented treatment options." However, while treatment options are described, there is no
analysis of survival outcomes. If feasible, I recommend adding an analysis of survival data to
strengthen the study's clinical relevance.
Review for 10.1186/s12876-025-03945-5 (2025)

Title: Unraveling the Site-Specific Features in Small Intestinal Stromal Tumors: A
Retrospective Study
Version: 2 Date: 11 Mar 2025
Reviewer:  Furkan Ali Uygur
Reviewer's report:
Dear authors, thank you for the work. I accept the decision to publish this work.
Decision: accept
Review for 10.1186/s12876-025-03945-5 (2025)

Title: Unraveling the Site-Specific Features in Small Intestinal Stromal Tumors: A
Retrospective Study
Version: 3 Date: 28 Apr 2025
Reviewer:  Ryosuke Sato
Reviewer's report:
The authors have appropriately revised the manuscript according to the comments.
Review for 10.1186/s12876-025-03965-1 (2025)

Title: Strain Elastography for Detecting Advanced Fontan-Associated Liver Disease: A
Retrospective Study
Version: 2 Date: 09 Apr 2025
Reviewer:  Amira A. A. Othman
Reviewer's report:
I want to extend my congratulations to all those involved in this work. All the required
amendments have already been made carefully and satisfactorily. I hope that the research will
be presented to science.
Review for 10.1186/s12876-025-03931-x (2025)

Title: Association of alkaline phosphatase to albumin ratio with all-cause mortality in critically
ill patients with cirrhosis: a retrospective study
Version: 1 Date: 28 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-As a retrospective study, the data are observational, and while the MIMIC-IV database is
comprehensive, it’s not possible to establish causality from these results. The findings should be
interpreted with caution regarding cause-and-effect relationships, especially since many factors
influencing mortality could not be controlled for.
-While it is good practice to exclude participants with more than 20% missing data to maintain
the integrity of the study, the exclusion of patients without ALP or ALB data (467 patients)
or those with missing demographic information (450 patients) may introduce selection bias.
The study may not fully represent the overall population of cirrhotic ICU patients due to these
exclusions.
-Despite controlling for a wide array of confounders, there could be unmeasured or residual
confounding factors. For instance, the severity of liver cirrhosis, which could vary widely among
patients, may not have been fully captured in the model. Furthermore, other biomarkers or
clinical parameters that could influence mortality may not have been included.
-While the APAR calculation is clear and easy to interpret, it’s important to consider whether this
ratio fully captures the complexity of cirrhosis progression or other factors influencing mortality.
There may be a need for further validation of the APAR index in different cohorts, particularly
outside the ICU setting.
-Despite adjusting for 26 covariates, there may still be unmeasured confounders influencing the
observed relationship. For example, the role of dietary factors, medications, or lifestyle habits
could affect both APAR levels and mortality risk, but these factors may not have been fully
captured in the analysis.
-While the study examines mortality at 28, 90, and 365 days, it would be useful to explore the
time-dependent nature of the association further. Mortality risk may vary over time, and a more
detailed exploration of time-to-event survival would enhance the understanding of how APAR
influences mortality risk in the short term versus the long term.
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 1 Date: 27 Feb 2025
Reviewer's report:
The manuscript explores the relationship between C. sinensis infection and gallbladder stone
disease, particularly focusing on the impact of infection on bile components, gallbladder
motility, and the formation of gallstones. The study investigates epidemiological correlations
and evaluates the morphology of C. sinensis eggs in gallbladder stones, bile sediment, and
bile samples. The authors also analyze the concentrations of various bile components and the
motility of the gallbladder in patients with GBSD, comparing those with and without C. sinensis
infection.
Major Comments:
1. It is mentioned in the manuscript that the percentage of male GSI patients is significantly
higher than that of female patients, and in Figure 2a it is shown that C. sinensis doesn’t seem
to be a risk factor for gallbladder stones in female patients. However, in the discussion section
doesn’t address possible reasons for this, such as the influence of sex hormones. Based on the
current findings, it seems difficult to explain why female patients are not affected by C. sinensis
infection in terms of its mechanism on gallbladder stone formation.
It is hoped that the authors will further explore and propose relevant hypotheses or explanations.
2. The manuscript concludes that C. sinensis infection, particularly the retention and calcification
of eggs, plays a crucial role in the formation of non-cholesterol gallstones in males. While the
study presents compelling data, the causal relationship between infection and stone formation
should be discussed more carefully. Calcification doesn’t necessarily mean that the eggs directly
caused the stone formation. Calcification may be a result of the stone formation process rather
than the sole causal factor.
The authors should clarify whether the morphological changes observed in the eggs (e.g.,
calcification) are a result of the infection itself or a consequence of the pathological environment
within the gallbladder.
3. The manuscript lacks discussion of potential confounding factors and other known risk factors
for GBSD (e.g., obesity, cholesterol levels). As mentioned in Table 2, 24 patients with C. sinensis
positive had cholesterol stones, whether confounding factors contributed to this stone formation.
These should be mentioned to provide a more comprehensive understanding of the study.
Overall Evaluation:
This study adds valuable information regarding the relationship between C. sinensis infection
and GBSD. However, the conclusions are somewhat overstated, and the manuscript would
benefit from more careful consideration of the limitations and a deeper exploration of the
mechanisms underlying the observed results. If the authors revise the manuscript to address
these concerns, it will be suitable for publication.
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 1 Date: 06 Mar 2025
Reviewer's report:
This article presents an interesting and important study on the association between Clonorchis
sinensis infection and the formation of gallbladder non-cholesterol stones in males in an endemic
area. The research question is relevant, and the findings contribute to our understanding of the
etiology of gallbladder stones in this specific population.
1. I noticed that the diagnosis of Clonorchis sinensis infection in the article was conducted using
the IgG antibody method, which involves a considerable amount of work. Has an effectiveness
evaluation been conducted for this method? Clinically, the microscopic examination of feces is
commonly used. If the two methods are combined, would the accuracy rate be higher?
2. The language of the article needs further refinement.
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 1 Date: 07 Mar 2025
Reviewer's report:
Dear Authors,
In my opinion, this is a very well-conducted and important study. However, I have some
suggestions for improvement.
Major:
1. Did men under 50 years of age in the highest risk group have concomitant diseases that could
affect the condition of the gallbladder? This includes conditions such as smoking, alcohol use
disorder, metabolic syndrome, type 2 diabetes, etc.
2. Could the lack of reliable results in women be attributed to a smaller sample size compared
to men?
3. Is it possible to calculate the correlation between the number of non-viable or dead eggs and
the severity of gallstone disease in men under 50 years of age with combined Clonorchis sinensis
infection? This could potentially serve as additional evidence.
4. Please include a separate discussion point addressing the clear potential mechanism of
gallbladder stone formation under C. sinensis infection.
Minor:
1. In the Introduction section, please provide supporting data for the statement: "Nevertheless,
little information on the impact of C. sinensis infection on the composition of bile and the
function of the gallbladder has been reported thus far."
2. Please include the ethical approval number and the date of approval in the text.
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 1 Date: 16 Mar 2025
Reviewer's report:
Thanks for your effort in the current research.
Why wasn't a stool analysis performed?
Were there cases already harbouring the adult parasities?
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 2 Date: 09 Apr 2025
Reviewer's report:
Dear Authors,
Thank you for taking the time to revise the manuscript. I have a few suggestions that might
further enhance the quality of your work.
1. While this may be a matter of personal preference, I recommend making the title smoother.
2. Please rewrite the Ethics Statement and the Participants and Specimens (1.) section to improve
clarity. Please clarify how the patient sample groups were formed. In one study, one group of
patients was used, while in another study, a different group of patients was used.
3. Who was selected for the "healthy medical examiners" group?
4. Please create a separate paragraph detailing the limitations of this study. Additionally, provide
more information about the patients in the Materials and Methods section, including their
comorbidities such as smoking, alcohol use disorders, chronic liver diseases, and other relevant
conditions. Ensure this information is clearly presented.
5. Please clarify how the different types of stones were classified.
6. In my opinion, the authors should mention the following paper:
DOI: 10.1017/S0022149X22000773.
Because similar information was previously presented in the paper, the data stating, "Through
microscopical examination of C. sinensis eggs and the material around them in gallbladder
stones, bile sediments, and bile, we discovered that the C. sinensis eggs participated in the stone
formation (Fig. 3)," is not new. The authors should rewrite this paragraph in the discussion
section.
7. In my opinion, the authors should cite the work by Luo XB et al., titled "Survey on Clonorchis
sinensis infection and bile component of gallstone patients from the Pearl River Delta region in
Guangdong Province," in the context of the presented data: "The results showed that the GSI
patients' bile had lower levels of TBA and CHO than that of the GP patients (P < 0.05), as seen
in Fig. 5." Similar information was previously observed by Luo and co-authors.
8. Please highlight the novelty and medical significance of this research, given that the main
finding—that C. sinensis eggs are involved in gallbladder stone formation—has been previously
published.
Review for 10.1186/s12876-025-03939-3 (2025)

Title: Formation of non-cholesterol gallstones in populations within clonorchiasis endemic
regions is closely related to Clonorchis sinensis infection
Version: 3 Date: 17 Apr 2025
Reviewer's report:
Dear authors,
Thank you for revising the manuscript point by point. I am now completely satisfied with
the current version of the manuscript and thank you for addressing all of my suggestions. I
recommend paying attention to typos in the main text.
Review for 10.1186/s12876-025-03869-0 (2025)

Title: Association between Dietary Inflammatory Index and Ulcerative Colitis: A Case-control
Study
Version: 1 Date: 21 Jan 2025
Reviewer's report:
Authors aims to confirm the causal relationship between DII and the onset of UC, as well as
the impact of DII on disease activity in UC patients, using a cross-sectional survey. The topic is
intriguing indeed, but there are some comments that need to be addressed or answered.
1.
The authors have conducted a cross-sectional survey of the dietary habits of individuals who
have already developed UC. To confirm whether DII is a cause of UC onset, data on DII before
the onset of UC is necessary, as the dietary habits could have changed after the onset of UC or
been modified in response to disease symptoms. Additionally, dietary habits change over time.
For these reasons, it seems difficult to assess a causal relationship regarding the onset mechanism
of UC based on a cross-sectional survey of individuals who have already developed UC.
2.
The aforementioned issue also applies when examining the relationship between DII and disease
activity. For those who are already experiencing exacerbation, their diet is likely to have changed
after a flare-up in terms of both content and intake. It would be more appropriate to longitudinally
assess whether differences in DII among individuals with similar background factors impact
future differences in disease activity. Furthermore, disease activity is likely to be strongly
influenced by other factors, such as current treatments and/or disease type.
3.
The authors state, “The correlation analysis between DII and UC was performed after adjusting
for confounders, which had a strong reliability.” However, in the text, only total energy intake
and use of medication are mentioned as covariate factors. Please specify all the confounding
factors that were adjusted for. Additionally, with only 106 cases (remission 50 / active 56), due
to the issue of overfitting, it seems that there may be limitations on the number of variables that
can be included in the regression model.
4.
Please consider factors such as age, sex, disease type, disease duration, UC treatment
medications, socioeconomic status as confounding factors between diet and UC disease activity.
5.
The authors state, “An Iranian study showed that UC was associated with increased DII (12).
Lamers demonstrated that the relationship between DII and disease activity is not significant in
UC,” and in this study, authors are also evaluating the same aspects as prior studies, namelly DII
and UC risk, as well as UC disease activity. Please clarify what the knowledge gap is between
DII and UC, and clearly state what the novelty of this study is.
6.
Please describe how the control group was selected. Was it matched based on any factors?
7.
Please add the information about comorbidities, and medications to Table 1. Similarly, for Table
2, please include important factors for confirming the causal relationship between DII and UC
disease activity such as disease type, disease duration.