JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-03617-4 (2025)

Title: Risk Factors for Organ-Space Surgical Site Infections After Minimally Invasive Rectal
Cancer Surgery: A Retrospective Cohort Study
Version: 4 Date: 21 Oct 2024
Reviewer's report:
Dear authors:
Thank you for the opportunity to review your interesting manuscript.
Most of your findings confirm findings of other groups and add valuable evidence in this field.
I wonder whether the higher incidence of  surgical site infection in the intersphincteric resection
group is related to the more difficult and prolonged dissection in these patients. Can you
comment on this please.
The same is true for the group 'hand-sewn anastomosis'.  As you state this was necessary in
patients where a linear stapler could not be used - certainly this has resulted in longer and
technically more challenging operations.  This would have contributed to a higher risk of SSI
as well.
It would be helpful to analyse the differences of the length of surgery with regard to  the effect
on SSI.  The increased  SSI rate in robotic surgery could also be related to the longer operating
times in these patients.
Please consider these comments for your resubmission.
Kind regards, Matthias Wichmann (FRACS)
Review for 10.1186/s12876-025-03617-4 (2025)

Title: Risk Factors for Organ-Space Surgical Site Infections After Minimally Invasive Rectal
Cancer Surgery: A Retrospective Cohort Study
Version: 4 Date: 01 Nov 2024
Reviewer's report:
good data set and analysis
please consider:
-add duration of surgery for assessment
-add types of intervention for organ space SSI eg antibiotics, percutaneous drain, return to OR
(eg. clavien dindo score)
Review for 10.1186/s12876-025-03617-4 (2025)

Title: Risk Factors for Organ-Space Surgical Site Infections After Minimally Invasive Rectal
Cancer Surgery: A Retrospective Cohort Study
Version: 4 Date: 09 Nov 2024
Reviewer:  Shoichi Fujii
Reviewer's report:
This study is an analysis of organ-space SSI after minimally invasive surgery for rectal cancer.
This is an analysis of a large number of cases and the results are thought to be important.
However, some corrections and additions are required.
1. How is this study different from studies that focus on anastomotic leakage? Isn't it simply a
risk analysis of suture leakage? If not, what percentage of organ-space SSIs other than pelvic
SSIs were present?
2. The definition of DM diagnosis is unclear.
3. Is operative time not a consideration?
4. Are there hand-sewn cases in CJP or TCP? Are there any confounding factors between CJP/
TCP and hand sewing?
5. What are the considerations behind the high incidence of organ-space SSI and bone
metastases? Nothing has been mentioned.
Review for 10.1186/s12876-025-03617-4 (2025)

Title: Risk Factors for Organ-Space Surgical Site Infections After Minimally Invasive Rectal
Cancer Surgery: A Retrospective Cohort Study
Version: 5 Date: 09 Dec 2024
Reviewer's report:
Dear authors - thank you for addressing the reviewers' comments and concerns. This additional
work has certainly improved the quality of your manuscript.
Kind regards, Matthias Wichmann
Review for 10.1186/s12876-025-03798-y (2025)

Title: A negative correlation of low estimated glucose disposal rate with significant liver fibrosis
in adults with NAFLD and obesity: results from NHANES 2017–2020
Version: 3 Date: 12 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03796-0 (2025)

Title: A mobile app to improve adherence to colorectal cancer screening and post polypectomy
surveillance guidelines
Version: 3 Date: 29 Jan 2025
Reviewer's report:
This study showed the potential of a mobile app aiding healthcare professionals in decision
making for adherence to CRC screening and post-polypectomy surveillance guidelines. Given
the low uptake of CRC screening in some countries, and the highly reported over- and underuse
of surveillance colonoscopy in several countries, this study is of great importance.
I have some comments for improvement:
1. I noticed that the authors mostly cite US-based studies. I guess this is a result from the high
number of literature from the US. However, in some cases (not all) it would be of value to cite
studies from the same or a similar health care system or culture as the data comes from (i.e.
studies from Spain or Europe).
For example,
a.  In the introduction section: “However, significant overuse and underuse of colonoscopy have
been reported in multiple studies [7-10]”
b. And discussion: “Concerning results from a study in the US showed that almost 20% of
American adults have never been screened for CRC [17].”
The authors may critically review the manuscript if this is also applicable to other parts of the
manuscript.
2. The problems of overutilization. In the introduction and discussion you address the burden
of overutilization. I agree with your arguments, but you may want to address that although rare,
overutilization might even harm patients, because of the invasive nature of colonoscopy.
3. Distribution, advertising and accessibility of the app is not clear. Please consider adding
information to the methods and/ or discussion.
4. The increase of app usage. In the results and discussion you refer to an increase of app usage.
Cumulative numbers increase, which is obvious, as they would only stagnate if usage ended.
But just from Figure 2, it is hard to see an increase of daily consultations. If there is one, please
also add some numbers to the text. If not, please rephrase.
5. Discussion: Avoidance/ savings of screening and surveillance.
a. As you don’t have actual data on how many persons would have utilized the procedures
without the app and how many avoided it because of the app, I would suggest “softer” wording,
e.g. instead of “(c) 68.2% and 50% of patients could avoid colonoscopy for CRC screening and
surveillance” -> “(c) in 68.2% and 50% of patients the app recommended to avoid colonoscopy
for CRC screening and surveillance and recommended FOBT instead”
b.  “69% savings in screening colonoscopies and 29% savings in post-polypectomy surveillance
colonoscopies”  -> I don’t understand where these numbers come from?
Minor:
Please note that there are several typos and errors in usage of upper and lower case. For example
2400 (13%) had history of first-degree CRC before de age of 50” and several minor errors in
Table 2. Please critically review the manuscript and correct further typos and errors.
Review for 10.1186/s12876-025-03796-0 (2025)

Title: A mobile app to improve adherence to colorectal cancer screening and post polypectomy
surveillance guidelines
Version: 3 Date: 07 Feb 2025
Reviewer's report:
This is a very good, well written retrospective analysis describing usage of mobile app helping
healthcare professionals to apply correct (according to regional guidelines) decisions concerning
commencing method of CRC screening, time of commencing it as well as post-polypectomy
surveillance intervals. Authors have proven that the app was widely accepted and used, that
allowed for correction of decisions concerning screening and surveillance. This app in my
opinion deserves to be used in other regions and countries modified if necessary for local
guidelines.
That’s why I think the manuscript needs to provide additional methodological information, e.g.:
how healthcare professionals were informed about the app, was the usage of the app anyhow
linked to reimbursement for procedures, how the GDPR rules were fulfilled for using the app
professionals.
Another minor issue is the list of authors on the title page (probably will be corrected by editors
when study is accepted) – there are currently different formats for different authors.
Review for 10.1186/s12876-025-03780-8 (2025)

Title: Relationship between anthropometric measures and the risk of incident Metabolic
dysfunction-associated steatotic liver disease: a longitudinal study
Version: 0 Date: 17 Nov 2024
Reviewer's report:
The author explored the relationship between several obesity indices and MASLD based on
gender differences, showing that BMI had the strongest predictive ability for MASLD in both
male and female populations. However, there are several shortcomings in the manuscript:
1. The introduction should be further refined to establish the significance of the study, such as
how this research fills the gaps in previous studies.
2. The research sample and design need to be described in more detail, including specifics of
the population recruitment.
3. In the multivariable logistic regression model, the author reports the odds ratio (OR) for each
unit increase in obesity indices (e.g., BMI, WC). However, if the relationship between these
indices and the dependent variable is non-linear, these ORs are meaningless.
4. The discussion section of this study does not adequately address the mechanisms underlying
the association between various obesity indices and MASLD.
5. The language needs further improvement, and the full name should be provided when
abbreviations are first introduced.
Review for 10.1186/s12876-025-03780-8 (2025)

Title: Relationship between anthropometric measures and the risk of incident Metabolic
dysfunction-associated steatotic liver disease: a longitudinal study
Version: 0 Date: 12 Dec 2024
Reviewer's report:
1.In the Introduction section, the authors' discussion of the association of anthropometric
indicators such as BMI, WC, BRI and ABSI with MASLD is inadequate. The validity of the
argument that BRI or ABSI are likely to be more useful than WC or BMI in predicting MASLD
events is not convincing. Please add appropriate evidence from the literature to further support
your view.
2.Please add a description of the inclusion exclusion criteria for the study population in the
methods section.
3.In the statistical analysis section, the authors describe adjusting for a range of confounding
variables including age and systolic blood pressure in the multiple logistic regression model, but
why were variables such as Diastolic blood pressure, AST, ALT, and GGT not included?
4.In the results section, the font formatting of the P-values is inconsistent, so please check the
full text for corrections.
5.This study used logistic regression to assess the longitudinal relationship between baseline
values of WC, BMI, BRI, and ABSI and incident MASLD stratified by sex. But why were
analyses stratified only by gender and lacked stratification by age?
6.The language of this paper lacks academic style.
Review for 10.1186/s12876-025-03780-8 (2025)

Title: Relationship between anthropometric measures and the risk of incident Metabolic
dysfunction-associated steatotic liver disease: a longitudinal study
Version: 2 Date: 21 Jan 2025
Reviewer's report:
The aim of this study was to investigate the association of body roundness index (BRI) and body
shape index (ABSI) with the occurrence of metabolic dysfunction-associated steatohepatopathy
(MASLD) in comparison with traditional waist circumference (WC) and body mass index
(BMI). The study evaluated the association of different anthropometric measures with the
development of MASLD by retrospectively analysing data from the Japanese Health Screening
Programme, and found that BMI was most significantly associated with MASLD, especially
in men, and provided the strongest predictive value for MASLD diagnosis. The study also
highlighted the need to develop specific waist circumference standards for Asian populations to
improve the diagnosis of MASLD. This study provides valuable data for exploring the use of new
body shape measures (BRI and ABSI) in metabolic dysfunction-associated steatohepatopathy
(MASLD), and in particular makes meaningful explorations in analysing gender differences.
Despite the limitations of retrospective and confounder control in the study design, its innovative
nature and potential contribution to clinical practice make it of academic value. Future studies
could further overcome these limitations and validate the clinical utility of these new metrics.
Based on the authors' responses and revisions to the five review comments, the manuscript's
deficiencies were largely addressed.
Review for 10.1186/s12876-025-03780-8 (2025)

Title: Relationship between anthropometric measures and the risk of incident Metabolic
dysfunction-associated steatotic liver disease: a longitudinal study
Version: 2 Date: 27 Feb 2025
Reviewer's report:
Congratulations on this important study. I found the topic very relevant and current. While
reading the article, comments, and responses it was possible to observe that the work has
improved. I only have a few suggestions for improvement:
1 - Remove the second "imaging" on p.4, line 65 to avoid redundancy.
2 - Regarding section "2.1 Study population and design", were there any further inclusion or
exclusion criteria applied to the study? i.e. age range or medical conditions.
3 - Please confirm if the ABSI p-value for males was <0.001. Although there was a difference
in dispersion, the medians were the same (0.076 vs. 0.076). This result is possible but I suggest
you review it.
4 - On p.10, lines 188-189 rewrite "whereas only ABSI was significantly associated in females"
to "whereas ABSI was only significantly associated in females".  The phrase as written means
that only ABSI was significant in the female sex (not other indices). The phrase corrected shows
that ABSI was only significant in the female sex (not in the male sex).
5 - In both p. 10, lines 189-190, and p. 13, lines 264-266, it should be explicitly stated that not
only BMI but also BRI and WC, were associated with MASLD.
Review for 10.1186/s12876-025-03780-8 (2025)

Title: Relationship between anthropometric measures and the risk of incident Metabolic
dysfunction-associated steatotic liver disease: a longitudinal study
Version: 5 Date: 11 Mar 2025
Reviewer's report:
The article provides important and original information concerning the association between
anthropometric measures and indices and the occurrence of metabolic dysfunction-associated
steatohepatopathy (MASLD).  After carefully reviewing the revised manuscript, I believe it is
ready for publication.
Review for 10.1186/s12876-025-03772-8 (2025)

Title: Increased intra-abdominal pressure linked to worse long-term prognosis among patients
with orthotopic liver transplantation: A retrospective, observational study
Version: 2 Date: 17 Jan 2025
Reviewer's report:
I am grateful for the opportunity to contribute to this compelling research. This study provides
valuable insights into the surgical outcomes of more than 380 liver transplants performed at
a single institution in China. The significance of this study lies in its innovative approach,
combining intra-abdominal hypertension (IAH) and the SOFA score as risk factors to predict
postoperative mortality. The detailed analysis of ICU data following liver transplantation is
commendable. However, while the study draws intriguing conclusions, there remains room for
further refinement.
1. Study Period and Outcome Measures
The study period for the target cases spans from January 2018 to March 2022. I believe the
observation period is insufficient to use 5-year survival as the primary outcome measure.
I recommend revising the outcome to either 3-month or 1-year survival, as these are more
appropriate given the available follow-up duration.
2. Donor Information in Prognostic Analysis
One key cause of intra-abdominal hypertension is a mismatch between graft size and recipient
physique (e.g., body surface area or BMI). However, Table 1 does not include donor-related
information. I suggest incorporating donor characteristics, including donor age, which is widely
recognized as a critical prognostic factor. It would be prudent to include donor age in the
multivariate analysis to enhance the robustness of the prognostic evaluation.
3. Univariate Analysis Results for Cox Regression (Figure 2)
In Figure 2, the authors perform a multivariate Cox regression analysis of overall survival (OS).
Given the small number of events (n=24), the study notes that factors were selected through a
stepwise approach as Figure 3. However, the univariate analysis results for all factors should
be presented alongside Figure 2 to provide transparency regarding the selection process and to
support the multivariate analysis.
4. AUC of SOFA Score (Figure 3)
In Figure 3, the SOFA score alone achieves a high AUC of 0.830, demonstrating strong
predictive power. Adding intra-abdominal pressure (IAP) results in only a marginal increase
to 0.834, which likely lacks statistical significance. This suggests that the simpler SOFA score
alone may be sufficient as a predictive tool.
5. Stratification of OS Risk Using Combined Factors
If the authors believe that combining IAH and the SOFA score offers added predictive value,
it is essential to present additional data supporting this claim. As both factors are identified as
independent risk factors for OS in the Cox regression analysis, devising a method to illustrate risk
stratification using these two factors would strengthen the argument. For instance, KM curves
according to these predictive factors or the cubic spline curves could visually demonstrate how
these factors interact to predict OS outcomes more effectively and determine the cut-off levels
of IAH.
Review for 10.1186/s12876-025-03772-8 (2025)

Title: Increased intra-abdominal pressure linked to worse long-term prognosis among patients
with orthotopic liver transplantation: A retrospective, observational study
Version: 3 Date: 03 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03772-8 (2025)

Title: Increased intra-abdominal pressure linked to worse long-term prognosis among patients
with orthotopic liver transplantation: A retrospective, observational study
Version: 3 Date: 03 Mar 2025
Reviewer's report:
The authors have correctly revised their manuscript and improved its quality to a level acceptable
to this journal.
Review for 10.1186/s12876-025-03784-4 (2025)

Title: Association between Atherogenic Index of Plasma and Chronic Diarrhea: A Cross-
Sectional Study of the NHANES 2005-2010
Version: 1 Date: 26 Feb 2025
Reviewer's report:
This is a Chinese paper investigating the association between the atherogenic index of plasma
(AIP), a marker of lipid metabolism, and chronic diarrhea (CD) in US adults using data from the
2005–2010 NHANES, finding a positive correlation between higher AIP levels and increased
risk of CD.
Comments
1. The cross-sectional design of the study does not allow to determine whether higher levels of
the AIP lead to CD or if CD causes changes in lipid metabolism. While the findings show an
association, they cannot prove causality.
2. Although the Bristol Stool Form Scale (BSFS) is a practical tool, it lacks the accuracy of a
clinical diagnosis by a gastroenterologist. This could result in some participants being incorrectly
classified as having or not having CD, potentially skewing the results.
3. The authors did not collect information on dietary habits, which are known to affect both lipid
levels and gut health. Without this data, it is difficult to rule out the possibility that diet may
have influenced the observed associations.
4. The authors excluded a large number of participants from the NHANES dataset due to missing
data on AIP, CD, or other key variables. This raises concerns about selection bias, as the final
sample of 5,785 individuals may not accurately reflect the broader US adult population.
5. The analysis did not consider the potential effects of medications, such as statins or
antidiarrheal drugs, which could impact both AIP and CD.
6. Genetic factors or environmental influences could have affected the results, and they should
be taken into consideration as confounders.
7. Since the authors are from China, it would be reasonable and useful to compare the results
from the US population with their own country, as the outcomes from the US population may not
apply to populations outside the US. Differences in diet, lifestyle, and healthcare systems could
alter the relationship between AIP and CD. Highlighting such potential differences in different
ethnic groups, may be more interesting to the international audience.
Review for 10.1186/s12876-025-03784-4 (2025)

Title: Association between Atherogenic Index of Plasma and Chronic Diarrhea: A Cross-
Sectional Study of the NHANES 2005-2010
Version: 3 Date: 13 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03799-x (2025)

Title: Prevalence and Characteristics of Adults Avoiding Gluten Without Celiac Disease: A
Long- Term Population-Based Follow-Up Study
Version: 0 Date: 19 Jan 2025
Reviewer's report:
The reviewer read with interest the paper titled "Prevalence and Characteristics of People
Avoiding Gluten Without Celiac Disease: A Long- Term Population-Based Follow-Up Study".
The authors analyzed the prevalence and possible predictive factors of people avoiding gluten
without celiac disease in two prospective cohorts from 2000 and 2011. The recruitment method
for the two samples reduces the risk of biases and allows for accurate data and information.
However, the main limitation of the study is that the results are dated. The most recent evaluation
is more than 10 years old, so it is unclear how representative it is of the current epidemiology
and situation. Nevertheless, since the data is so accurate and shows an interesting increase in
the past, the reviewer would suggest presenting the results as a research letter rather than as an
extensive study.
Moreover, the reviewer would suggest better clarification of the numbers in brackets in the first
rows of the results to improve readability and comprehension.
Additionally, Table 3 should be simplified, as it is currently not easy to read.
Review for 10.1186/s12876-025-03799-x (2025)

Title: Prevalence and Characteristics of Adults Avoiding Gluten Without Celiac Disease: A
Long- Term Population-Based Follow-Up Study
Version: 1 Date: 22 Feb 2025
Reviewer's report:
Thanks to the authors for responding to the previous comments. I acknowledged this, but I still
feel that the data is really dated and not matched with the current situation of the limited number
of people who avoided gluten back in 2000 and 2011 as compared to the people in 2025.
Review for 10.1186/s12876-025-03791-5 (2025)

Title: Clinical value of using double balloon enteroscopy combined with endoscopic ultrasound
to evaluate Crohn’s disease of the small bowel: a retrospective study
Version: 0 Date: 11 Jan 2025
Reviewer's report:
The manuscript offers valuable insights into diagnosing small bowel Crohn’s disease but
requires revisions to address specific weaknesses. The authors should improve the discussion,
acknowledge the study's limitations, and enhance data presentation. With these changes, the
manuscript has the potential for significant clinical impact.
Abstract: Clarify the specific advantages of the proposed method over other imaging techniques
in the "Results" section.
Introduction: Provide more background on the challenges of diagnosing small bowel Crohn's
disease with existing modalities.
Methods: Expand on the training of the physician performing the procedures to emphasize
consistency and accuracy.
Results: Include confidence intervals for key measurements (e.g., bowel wall thickness).
Discussion: Elaborate on the potential for endoscopic ultrasound to guide therapeutic decisions,
such as identifying candidates for biologic therapy.
Figures and Tables: Add graphical representations to improve data visualization.
Review for 10.1186/s12876-025-03791-5 (2025)

Title: Clinical value of using double balloon enteroscopy combined with endoscopic ultrasound
to evaluate Crohn’s disease of the small bowel: a retrospective study
Version: 0 Date: 26 Jan 2025
Reviewer's report:
Thank you for the opportunity to review your interesting paper. This manuscript presents
compelling data on the usefulness of EUS using DBE for evaluating disease activity in small-
bowel lesions of CD patients. The main research findings are important and can contribute to
the clinical management of CD patients. While the manuscript is well written, there are several
issues that need to be addressed. Below are this reviewer’s comments:
Major Comments
#1. The authors should clearly specify how the endoscopic findings compare with the EUS
findings. The central question that this paper should emphasize is whether the addition of EUS
enhances disease assessment compared to the mucosal findings from DBE alone.
#2. To better illustrate the usefulness of EUS, the inclusion of reference images from EUS would
be highly beneficial for readers.
#3. The relationship between HBI and mpSES-CD, presented in Table 1, could be made clearer
by illustrating the correlation in a figure rather than a table.
#4. The analysis in Table 3 uses the chi-square test and includes the statement: “Still, it was
significantly lower in patients with severe disease activity.” Given the small sample size, Fisher's
exact test may be more appropriate. Additionally, while significant differences in proportions
are noted among the three groups, it is unclear which group has the highest proportion. Multiple
comparisons or a residual analysis would be necessary to support such conclusions statistically.
#5. How do EUS findings correlate with prognosis? Results showing that EUS findings are more
useful than endoscopic findings in predicting recurrence would add significant novelty to the
paper.
#6. Were correlations examined with biomarkers such as CRP, LRG, and fecal calprotectin, in
addition to HBI? These relationships could strengthen the study's findings.
#7. The limitations of the study are not discussed in the Discussion section and should be
included.
Minor Comments
The specific DBE and EUS models used in this study should be listed in the Examination
Methods section.
Review for 10.1186/s12876-025-03765-7 (2025)

Title: Factors influencing the incidence of early gastric cancer: A Bayesian Network analysis
Version: 1 Date: 14 Dec 2024
Reviewer's report:
This study assesses and predicts the risk of gastric cancer based on 1,820 high-risk individuals,
using Lasso regression and Bayesian network predictive models. Overall, the structure is clear,
and the results are solid. The work can be considered for publication after revision. Below are
my comments:
1. While I understand that the authors used Lasso regression to select factors, I believe some basic
demographic factors (e.g., Gender, Age) should be forced into the Lasso regression and Bayesian
network predictive models. I leave it to the authors to decide whether additional demographic
factors should be included. The "glmnet" package may offer an option to incorporate this
constraint.
2. In the Results section, I suggest omitting the cross-validation plot that shows how the optimal
number of indicators (7) was selected. Instead, I am more interested in seeing the coefficients and
other relevant information for each factor in the Lasso regression or standard linear regression.
The current cross-validation plot can be either retained or moved to the supplementary material.
3. I could not find where Table 1 is included in the main text. Additionally, more details should be
provided to describe the demographic characteristics. It would be helpful to compare each factor
between GC patients and non-GC patients using the appropriate statistical tests and provide the
corresponding P-values in Table 1.
4. The description of the results is too brief. More details should be added, including the
motivation behind each analysis. I suggest avoiding the use of "analysis models" as subsection
titles. Instead, the titles should focus on the research question being addressed.
5. In the tables, the authors summarize many factors. However, the definitions of several
variables (e.g., smoking) are missing. I recommend adding definitions for some of the variables
in the supplementary material or within the main text.
6. For each figure, the legend should not merely contain a short title. It should include
more detailed information about how the results were generated. The figure legend should be
comprehensive enough to allow readers to interpret the figure without needing to refer to the
main text.
7. For Figures 2 and 3, please improve the resolution and make the text clearer.
Review for 10.1186/s12876-025-03765-7 (2025)

Title: Factors influencing the incidence of early gastric cancer: A Bayesian Network analysis
Version: 1 Date: 24 Dec 2024
Reviewer:  Sajad Shafiekhani
Reviewer's report:
Dear Editor
I would like to thank you for passing this manuscript to me for review.
The manuscript is about prediction of gastric cancer by LASSO regression according to clinical
features. So many machine learning models can be used for determining which features are best
predictors of GC (feature selection methods such as MRMR, NCA,...) and so many classification
models can be used to classify GC from non-GC individuals. I propose to expand modeling
aspect of this study and compare and validate the results by comparing that with results of other
methods (such as methods I mentioned).
I recommend major revise.
I have some comments may help improve the manuscript:
1- introduction can be improved if pay attention to studies with aim to predict risk factors related
to gastric cancer and make a comprehensive report of their results.
2- In methods: Only Bayesian network was used to discriminate gastric cancer from non-gastric
cancer patients, while so many classification models such as SVM, KNN, Tree, Ensemble and
other can be implemented and outperformed Bayesian model of this study with .615 AUC. I
propose to use feature selection methods to find top scored predictors of GC and compare the
results with LASSO.
Review for 10.1186/s12876-025-03765-7 (2025)

Title: Factors influencing the incidence of early gastric cancer: A Bayesian Network analysis
Version: 2 Date: 25 Jan 2025
Reviewer:  Sajad Shafiekhani
Reviewer's report:
Dear Editor
The models implemented are not able properly predict both positive and negative cases because
of low sensitivity and specificity values, for example in SWSFS-BN method, the specificity
and sensitivity are 0.18 and 0.89 respectively and in Lasso-BN these values are 0.97 and
0.13 respectively. Maybe a method of voting between model predictions can use both high
sensitivity and high specificity power of different methods and generate an ensemble model with
high sensitivity and high specificity values. I recommend share data as supplementary file and
recommend in discussion for further analysis by interested researchers to do more analysis on
dataset. I recommend accept.
Review for 10.1186/s12876-025-03744-y (2025)

Title: Association Between Dietary Potassium Intake and the Prevalence of Gallstones in
American Adults: an Assessment of Data from the National Health and Nutrition Examination
Survey#########################################
Version: 2 Date: 02 Jan 2025
Reviewer's report:
The authors aim to explore an interesting and relatively less-studied area in their work—the
impact of potassium intake on gallstone formation. The study is well-organized and structured,
with the statistical rigor being particularly commendable. However, several minor revisions are
required to unlock the full potential of this work, which is inherently present.
1. The most significant shortcoming is the modest presentation of the clinical applicability of the
findings. The manuscript should emphasize more strongly the potential therapeutic opportunities
that could arise in the future from rationalizing potassium intake. This would not only enhance
the impact of the results but also provide a clearer vision for the practical implications of the
study.
2. The authors' affiliations are unclear in the main text. Do they all belong to the same institution?
3. The types of gallstones are mentioned only tangentially; however, the listing and
categorization are unprofessional and difficult to understand. A more precise and clear execution
is necessary.
4. The overall incidence of gallbladder cancer is relatively low, even among those with
gallstones. If you're referencing this in a detailed or professional context, it may be helpful to
include specific data or more citations to strengthen the point.
5. The role of different ions and salts in gallstone formation? Such as calcium? It would be
noteworthy to include authors and references not connected to the aurhors.
6. Why is the limit set at 20 years?
7. How can be the two Figure 1 in the main text?
8. The patient's self-reported gallstone condition carries a high risk of bias. Although it is
mentioned tangentially in the limitations, this aspect needs to be emphasized much more
strongly.
9. The legend of Figure 2 mentions that only 98% of the data is represented in the figure, but
no explanation is provided. It is possible that this is addressed in the text; however, it should
also be clearly stated in the legend.
10. What specific mechanism could link potassium intake to the development of gallstones? The
text does not provide a concrete explanation for this, although several correlating factors, such
as T2DM are listed. Could the relaxation of the gallbladder wall play a role, or perhaps some
other process?
11. Additionally, is there a difference based on the type of gallstone? It is possible that the
process may have a stronger effect on one type of stone compared to another. This information
must be included for a comprehensive analysis.
12. A more detailed (and maybe separated) limitation section is required.
13. The draft is formally organized and cohesive; however, it contains numerous typographical
and grammatical errors (e.g., missing or double spaces, missing letters, compound word issues,
incorrect verb tenses). A thorough review by a language editor is necessary.
Review for 10.1186/s12876-025-03744-y (2025)

Title: Association Between Dietary Potassium Intake and the Prevalence of Gallstones in
American Adults: an Assessment of Data from the National Health and Nutrition Examination
Survey#########################################
Version: 2 Date: 18 Jan 2025
Reviewer's report:
This study has a clear structure, but there are several points where it can be improved. Here are
some weaknesses:
1. The connected words, unfinished sentences, and missing letters need to be corrected.
2. It mentions a "paucity of current epidemiological research" but does not provide context on
existing studies or gaps in the literature. It does not clearly emphasize why this research question
is novel or how it builds on previous findings.
3. The authors do not address the recommendations for dietary potassium intake, >3500 mg
vs. #3500 mg - the optimal potassium intake recommended by organizations such as the World
Health Organization has been defined as #3500 mg per day. Define the cut-off values for the
tertiles of potassium intake listed in the results.
4. The key observation is that the results need to be adjusted for diuretic (thiazide diuretic) intake
due to potassium losses.
5. In conclusion: The statement "highlighting the significance of dietary factors in the prevention
of gallstones" is too broad and is not supported by the data presented. The study focuses only
on potassium, not on all dietary factors.  The sentence "In the group of Americans aged 20 and
older" does not fit seamlessly into the context and seems disjointed.
Review for 10.1186/s12876-025-03781-7 (2025)

Title: Validation of the diagnostic accuracy of the acFibroMASH index for at-risk MASH in
patients with metabolic dysfunction-associated steatotic liver disease
Version: 2 Date: 06 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03763-9 (2025)

Title: Optimizing Outcomes in Acute Pancreatitis: The Impact of of Heparin Therapy Duration
on Mortality in a Multi-Center Retrospective Study
Version: 1 Date: 24 Feb 2025
Reviewer:  Vincenzo Neri
Reviewer's report:
Optimizing Outcomes in Acute Pancreatitis: The Impact of of Heparin Therapy Duration on
Mortality in a Multi-Center Retrospective Study
The Abstract clearly summarizes the contents of the clinical study.
The introduction is correct and frames well the possible therapeutic role of heparin with the
choice of timing of administration in severe pancreatitis.
The Methods with the sections Study design and patients, Data collection, Study outcome,
Statistical analysis, are fully described.
The results are credible and appropriate to the complex approach of the study.
The discussion is developed in a complete and correct manner, highlighting the hypothesis of
the mechanism of action of heparin.
The conclusions are appropriate to the development of the study.
The References are updated and adequate.
The tables and figures are clear and useful in reading and understanding the text
Review for 10.1186/s12876-025-03763-9 (2025)

Title: Optimizing Outcomes in Acute Pancreatitis: The Impact of of Heparin Therapy Duration
on Mortality in a Multi-Center Retrospective Study
Version: 2 Date: 28 Feb 2025
Reviewer's report:
I have carefully reviewed the revised manuscript and the authors' responses to my comments.
I am pleased to confirm that the authors have addressed all of my concerns and questions in a
satisfactory manner. I recommend accepting the manuscript in its current form.
Review for 10.1186/s12876-025-03763-9 (2025)

Title: Optimizing Outcomes in Acute Pancreatitis: The Impact of of Heparin Therapy Duration
on Mortality in a Multi-Center Retrospective Study
Version: 2 Date: 01 Mar 2025
Reviewer:  Vincenzo Neri
Reviewer's report:
The manuscript is of excellent quality
Review for 10.1186/s12876-025-03783-5 (2025)

Title: Magnet-assisted diverticuloplasty for treating the symptomatic esophageal diverticulum:
a case series (with video)
Version: 2 Date: 22 Jul 2024
Reviewer's report:
Changes in the word attached, revise accordingly. Also, do not call your paper study. It is a case
series. Be consistent thoughout
Review for 10.1186/s12876-025-03783-5 (2025)

Title: Magnet-assisted diverticuloplasty for treating the symptomatic esophageal diverticulum:
a case series (with video)
Version: 2 Date: 06 Sep 2024
Reviewer:  Mohamed Hashim
Reviewer's report:
In spite of limitations of the study, it is a novel study and can be considered a pilot study.
The  retrospective nature, small number of sample size, make limitation of the results.
Review for 10.1186/s12876-025-03783-5 (2025)

Title: Magnet-assisted diverticuloplasty for treating the symptomatic esophageal diverticulum:
a case series (with video)
Version: 2 Date: 06 Sep 2024
Reviewer:  Ali S. Taha
Reviewer's report:
Ruide Liu et al. Magnet-assisted diverticuloplasty for the treatment of the symptomatic
esophageal diverticulum: a case series study.
This series of case reports or retrospective study aimed to explore the effectiveness and safety
of magnetic compression technique (MCT) in the treatment of oesophageal diverticula in 6
patients. The techniques was successful in all cases and this was associated with resolution of
the presenting symptoms as measured by the Eckardt symptomatic scores.
The strengths and limitations are fairly described in the Discussion.
My only suggestion is for the authors to mention the symptoms of oesophageal diverticulum
in the Introduction, including dysphagia, chest discomfort, regurgitation and weight loss. These
are mentioned in Table-3, but it is better for the readers to be informed of them right from the
beginning of the article in order to understand the justification of the proposed technique.
Review for 10.1186/s12876-025-03783-5 (2025)

Title: Magnet-assisted diverticuloplasty for treating the symptomatic esophageal diverticulum:
a case series (with video)
Version: 4 Date: 27 Feb 2025
Reviewer:  Mohamed Hashim
Reviewer's report:
The authors responded to the reviewers  comments.
Review for 10.1186/s12876-025-03783-5 (2025)

Title: Magnet-assisted diverticuloplasty for treating the symptomatic esophageal diverticulum:
a case series (with video)
Version: 4 Date: 27 Feb 2025
Reviewer:  Ali S. Taha
Reviewer's report:
Thanks for revising the manuscript taking into account my comments
Review for 10.1186/s12876-025-03785-3 (2025)

Title: Diagnostic performance of contrast-enhanced CT combined with contrast-enhanced MRI
for colorectal liver metastases: A case-control study
Version: 1 Date: 02 Feb 2025
Reviewer's report:
Dear authors,
This is obviously already a revised version of the manuscript. However, both the manuscript
itself and a reply to the first review should meet certain formal requirements. This is certainly
not the case for the response letter.
The correspondence addresses, e.g. superman_357@163.com, also lack a certain seriousness?
Why is there no institute address used? Furthermore, the question arises as to why there is no
clinical trial number and no consent for publication.
However, the study is otherwise methodologically ok and the results are not surprising.
Nevertheless, I think that most cases can be clarified using MRI only.
This is probably also practiced in many countries. In most cases, however, a staging CT or PET/
CT is performed beforehand and when there is a questionable finding in the liver. The planned
dual use of MRI and CT will certainly not become established in routine clinical practice, but
will be reserved for individual cases.
The sample size estimation section is very confusing and certainly needs to be edited. The
formula cannot be read in its present form and the variables cannot be assigned. The only
question is whether this is actually needed at all.
What does the “Deceleration” section mean after the discussion?
All in all, there is still a lot that needs to be changed before the manuscript can be published.
Review for 10.1186/s12876-025-03785-3 (2025)

Title: Diagnostic performance of contrast-enhanced CT combined with contrast-enhanced MRI
for colorectal liver metastases: A case-control study
Version: 1 Date: 04 Feb 2025
Reviewer's report:
Thank you for asking to review this manuscript.
There are many articles that have looked at comparison between MRI and CT for diagnosis of
liver metastases. In this regard the manuscript offers nothing new.
There are several major problems with this study.
Many vague terms are used instead of clear definitions. Terms such as thorough review,
sophisticated case-control matching etc. are too subjective
The reference test is not defined.
It is not clear whether sensitivity and specificity is per lesion or per case.
It is not clear how much time had gone between MRI and CT. Which one was done first if long
time had gone between the scans.
The authors' recommendation to do both RI and CT is not appropriate as a general rule. In a
patient with wide spread disease  and with no doubt about diagnosis on one modality there would
be very little to gain by doing both scans. Conversely in patient who is potential candidate for
curative intent surgery or with inconclusive results on one scan complementary scan is very
useful.
This is a retrospective study. It begs the question why MRI and CT done for these patients
initially? Is this routine at the institution of the authors? or was this chosen because of special
circumstances. The latter case can lead to inclusion bias.
Some minor problems are
The introduction is too long and redundant.
Some reference are too old.
what does both radiologists going through training and calibration exercise mean?
The highest b-value used by the authors was 450 which is somewhat low for liver imaging.
No illustrative images.
There is a lot of repetition of introduction in discussion.
Review for 10.1186/s12876-025-03785-3 (2025)

Title: Diagnostic performance of contrast-enhanced CT combined with contrast-enhanced MRI
for colorectal liver metastases: A case-control study
Version: 1 Date: 06 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-While retrospective studies are common for this type of research, they are prone to selection bias
and confounding factors that can influence the results. The authors mention that convenience
sampling was used, which may not be representative of the broader population. A prospective
study design could minimize such biases and provide stronger evidence.
-Although the use of matching methods helps control for some confounders, the reliance on
convenience sampling limits the generalizability of the results. A more randomized sampling
approach would increase the external validity of the findings.
-The study focuses primarily on diagnostic accuracy without assessing the impact of the imaging
modalities on clinical outcomes such as treatment decisions, patient survival, or recurrence
rates. Long-term follow-up data would provide valuable insights into how multimodal imaging
influences therapeutic planning and patient prognosis.
-The study focuses on diagnostic accuracy but does not address the potential cost-effectiveness
of combining CT and MRI. Given that combining these imaging modalities could increase
healthcare costs, it would be useful to discuss whether the improvement in diagnostic accuracy
justifies the added expense, especially in resource-limited settings.
-While the discussion highlights statistical significance in diagnostic accuracy, it would be
beneficial to discuss the clinical significance of these findings more explicitly. For instance,
how much earlier could MRI potentially detect metastases compared to CT? Are there specific
subgroups of patients who would benefit most from MRI, such as those with small lesions or
early-stage metastases? Providing more context about how the differences in sensitivity and
specificity might translate to real-world clinical practice could make the results more tangible
for readers.
-The combined use of CT and MRI is mentioned as enhancing diagnostic accuracy, particularly
in detecting small lesions, but the discussion could elaborate further on why combining
these modalities leads to higher diagnostic confidence. It would also be helpful to explore
potential drawbacks or challenges in clinical practice when using combined imaging (e.g., added
costs, increased time for interpretation, or patient burden) and how these could be addressed.
Discussing the specific benefits of combining both modalities could strengthen the argument
for adopting this approach.
Review for 10.1186/s12876-025-03785-3 (2025)

Title: Diagnostic performance of contrast-enhanced CT combined with contrast-enhanced MRI
for colorectal liver metastases: A case-control study
Version: 1 Date: 09 Feb 2025
Reviewer's report:
This manuscript presents a well-conducted case-control study evaluating the diagnostic
performance of contrast-enhanced CT and MRI in detecting colorectal liver metastases (CRLM).
The study design, methodology, and results are clearly presented, and the findings highlight
the significant improvement in diagnostic accuracy when combining both imaging modalities.
However, there still are some weaknesses should be revised.
1. Gadoterate meglumine (extracellular non-specific contrast agent) was used for enhanced MRI
in this study, however, hepatocyte-specific contrast agents is recommended in the guidelines
to improve the detection rate of metastatic lesions. Please explain in detail and compare with
previous literature.
2. The manuscript does not provide a detailed explanation of the gold standard criteria for
diagnosing liver metastases. Were all specimens obtained through surgical resection or biopsy?
3. In this study, the maximum b-value used for DWI was only 450 s/mm², and lower b-values
could potentially result in reduced sensitivity for detecting liver metastases.
3. Please specify the time interval between the administration of the two contrast agents. The
use of both CT and MRI contrast agents raises concerns about the increased risk of contrast
nephropathy, which is an important factor to consider in clinical practice.
4. While the study demonstrates improved diagnostic accuracy, the discussion could benefit
from a more detailed exploration of the clinical implications, such as how the combined imaging
approach might influence treatment decisions and patient outcomes.
5. The retrospective nature of the study may introduce selection bias. And, the study was
conducted at a single institution, which may limit the generalizability of the findings.