JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
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: 29 Jan 2025
Reviewer's report:
Review
Association between Dietary Inflammatory Index and Ulcerative Colitis: A Case-control Study
General comments:
Thank you for letting me review this interesting article. Dietary studies are challenging to
perform, and the official guidelines are often controversial based on newer updated science
challenging established truths. The study design is good.
Generally well understood English, but further professional language processing is strongly
recommended for a better flow and word selection. I have not corrected this manuscript for
potential language improvements.
Illustration of different included diet grouping and their DII score is requested.
My statistician prefers this method of presenting: (OR=4.921, 95% CI [2.27, 10.65])
Recommend using only two fractional digits: Ex: 4.921 # 4.92
I recommend changing this consistently throughout the article.
OBS: phrase patients with IBD and not IBD patients.
The tables seems to present the results correctly. The formatting is not ideal after downloading.
Parts of the introduction and discussion phrases statements that are inaccurate according to
gastroenterology and internal medicine knowledge. More and better references are needed.
For the discussion: start with your results and then link them to previous results. Finally, you
can include theories of why DII etc is important for UC/inflammation and suggest what kind
of diet is recommended.
Conclusion: Major revision
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: 01 Feb 2025
Reviewer:  Yasmine Y. Bouzid
Reviewer's report:
Reviewer Report
The manuscript titled “Association between Dietary Inflammatory Index and Ulcerative Colitis:
A Case-control Study” uses patients with ulcerative colitis and healthy controls to assess
associations between inflammatory potential of the diet and UC. I would like more information
on the dietary assessment. Some of the results are overstated for a retrospective case-control
study. Comments for the authors are included here:
1. As far as statistical methods, please consider calculating nutrients per 1000 calories to display
diet composition proportional to energy intake (Table 3.2). The UC cases seem to eat less
than controls (nearing statistical significance) and I question whether intake of certain nutrients
appears higher due to greater overall intake. I wonder the effect of UC symptoms on appetite
if you could discuss.
2. Please consider calculating adjusted p-values using the Benjamini Hochberg method: https://
academic.oup.com/jrsssb/article/57/1/289/7035855?login=false. Many nutrients are assessed,
and it is wise to correct for multiple hypothesis testing.
3. For what period were participants asked to estimate their dietary intake? The last year? The last
6 months? Food frequency questionnaires are semi-quantitative and require that study personnel
specify the time for which participants are to estimate their dietary patterns. It’s important to
know the recall period for a retrospective study.
4. Results did not show a significant difference between DII in active UC cases and those in
remission, thus it is overstated to say dietary changes can help cases achieve remission (Line
199-200).
5. “UC risk, incidence, or occurrence” cannot be assessed by the retrospective study design.
Participants did not develop UC during the study period, and without clarification of the period
the FFQ was used to assess, we cannot extrapolate participants’ diet patterns at the time they
developed UC. The design is cross-sectional, therefore only associations can be stated for the
time when dietary data and gastrointestinal health information were collected.
6. Please ensure that wording is consistent for Dietary Inflammatory Index. It’s stated several
times as ‘dietary inflammation index’.
7. Consider stating the limitation that the DII was developed using literature on associations
between diet and systemic inflammation markers, but not gastrointestinal markers.
Review for 10.1186/s12876-025-03869-0 (2025)

Title: Association between Dietary Inflammatory Index and Ulcerative Colitis: A Case-control
Study
Version: 2 Date: 17 Feb 2025
Reviewer's report:
There are no tracing of changes in the document or response letter for reviewers which makes
the review process difficult. I will request this before I will preceed further.
Review for 10.1186/s12876-025-03869-0 (2025)

Title: Association between Dietary Inflammatory Index and Ulcerative Colitis: A Case-control
Study
Version: 3 Date: 18 Mar 2025
Reviewer's report:
The manuscript addresses an important topic and presents results that contribute to clinical
practice. I have a few questions about the methodology. The authors adjust the analyses for total
energy intake, but it is not clear whether they use the residual method to calculate daily nutrient
intake. The residual method is a common method when calculating nutrient intake. If they do use
it, they would be adjusting twice for energy. I also have a few suggestions that would improve
the manuscript.
Introduction
Page 2, lines 38-39:  This statement is a subject of some controversy; therefore, it is essential
that it be supported by references from reliable sources.
“Studies have shown that intake of a diet high in omega-3 polyunsaturated fatty acids may have
a protective effect against UC.”
Page 2, lines 57-59: I suggest making it clearer that this is a study that involves an adult
population in the objective of the study, for example.
Results
Page 4, lines 138 – 144: The same information was presented twice in the same paragraph ("...50
were in remission..." and "...remission phase (47.17%)..."), I suggest reviewing this.
Page 9, lines 164-166: I suggest moving the following sentence to the methods section on
statistical analysis.
“Adopting a more conservative statistical significance threshold, adjusted p-values were
calculated using the Benjamini Hochberg method, and the significant results were consistent
with those when unadjusted.”
Page 11, table 3: In the Niacin nutrient row, in the control column, there is the word “control”
in the middle of the table.
Review for 10.1186/s12876-025-03918-8 (2025)

Title: Identification of the "Collagen-Macrophage" sub-category of patients with colorectal
cancer as an extension of the CMS4 subtype with THBS2 as a therapeutic target
Version: 3 Date: 23 Feb 2025
Reviewer's report:
Major
1. Please better clarify how the proposed "Collagen-Macrophage (CM)" subclass extends
beyond the CMS4 classification. Please  emphasize the practical implications of this new
subclass in clinical settings.
2. THBS2 is proposed as a key biomarker, however its not clear whether validation across
independent datasets or prospective clinical cohorts is performed or not. If not please add this
as limitations to emphasize the role of external validation for stronger translational relevance.
3. The description of single-cell sequencing methodologies and cell clustering lacks clarity.
Providing more methodological details on normalization, batch correction, and cell annotation
would enhance reproducibility.
4. The manuscript mentions a correlation between the CM-clustering differential gene score
(CSDGS) and TIDE score, but the biological rationale behind this correlation should be
discussed in greater depth.
5. The study suggests that blocking THBS2 improves PD-1 therapy. However, more direct
evidence, such as immune infiltration assays post-treatment, is necessary to substantiate these
claims.
6. Please better clarify how the multiplex immunohistochemistry images have been quantified
and statistically analyzed to strengthen claims regarding the spatial localization of FAP+ CAFs
and SPP1+ macrophages.
7. Please explain how the authors considered potential confounders. Given the heterogeneity
of CRC, factors such as microsatellite instability status, mutation burden, and immune profiles
should be controlled when defining CM classification.
8. Please clarify whether the Kaplan-Meier survival curves are adjusted for clinical covariates
to ensure the association is independent of other prognostic factors or not.
Minor
9. Please improve the annotations, legends of figures (e.g., UMAP plots) to better interpret CM
vs. non-CM differences.
Review for 10.1186/s12876-025-03918-8 (2025)

Title: Identification of the "Collagen-Macrophage" sub-category of patients with colorectal
cancer as an extension of the CMS4 subtype with THBS2 as a therapeutic target
Version: 5 Date: 31 Mar 2025
Reviewer's report:
The authors have adequately addressed all my previous concerns. I appreciate their response
and I have no further comments.
Review for 10.1186/s12876-025-03918-8 (2025)

Title: Identification of the "Collagen-Macrophage" sub-category of patients with colorectal
cancer as an extension of the CMS4 subtype with THBS2 as a therapeutic target
Version: 5 Date: 13 Apr 2025
Reviewer's report:
The author's response to the previous review comments is satisfactory, and I recommend the
article for publication
Review for 10.1186/s12876-025-03859-2 (2025)

Title: Association between adhering to a dietary approach to stop hypertension and risk of
colorectal cancers: A systematic review and meta-analysis
Version: 1 Date: 30 Jan 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-Although the introduction outlines the components of the DASH diet, it would benefit from
a brief mention of possible biological mechanisms linking DASH diet adherence to CRC
prevention. For instance, how might the DASH diet impact inflammation, gut microbiota, or
oxidative stress—key factors in cancer development?
-The introduction could benefit from highlighting more directly the gap in the literature
regarding the DASH diet and CRC prevention. This would strengthen the argument for
conducting the systematic review and meta-analysis.
-While the inclusion criteria are well-defined, it would be helpful to mention what types of
observational studies are being included. For example, are both case-control studies and cohort
studies acceptable? This level of specificity can aid in the reproducibility and clarity of the
review process.
-Subgroup analyses based on factors like gender, geographical location, and study design are
mentioned, but it would be beneficial to elaborate on how these subgroups are expected to
influence the results. For example, are there specific reasons to believe that gender or region
might alter the effect of the DASH diet on CRC risk?
-While the authors mention the gender differences observed in the results, a more detailed
exploration of why such differences might occur would enhance the discussion. For example,
are there hormonal or lifestyle factors that could explain why the DASH diet is more protective
in men than in women in certain studies? A deeper dive into this could strengthen the paper’s
conclusions on this point.
-While the authors mention that subgroup analyses were conducted, it would be helpful to
have more detailed results from these analyses. For instance, which factors (e.g., geographical
location, socioeconomic status, baseline diet) showed the most significant heterogeneity in the
results? Presenting these details could provide more context for understanding the variability
in outcomes.
-While some confounders like physical activity and lifestyle behaviors are briefly mentioned,
a more comprehensive discussion of potential confounders would be beneficial. For example,
how might underlying comorbidities (e.g., diabetes, hypertension) influence the observed
relationship between DASH adherence and CRC risk? A more in-depth exploration of these
variables could further clarify the diet's role.
Review for 10.1186/s12876-025-03859-2 (2025)

Title: Association between adhering to a dietary approach to stop hypertension and risk of
colorectal cancers: A systematic review and meta-analysis
Version: 3 Date: 21 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory.
Review for 10.1186/s12876-025-03859-2 (2025)

Title: Association between adhering to a dietary approach to stop hypertension and risk of
colorectal cancers: A systematic review and meta-analysis
Version: 3 Date: 27 Feb 2025
Reviewer's report:
1) The authors should include the PRISMA checklist as part of the supplementary material.
2) It is recommended that the authors update their search strategy to ensure it is current.
3) For cohort studies, the authors should utilize the ROBINS-E tool for risk of bias assessment,
as it is a more appropriate tool compared to NOS.
4) The authors should specify which heterogeneity estimator was used in their analysis.
5) The authors should implement and present the GRADE approach.
6) The data analysis has been conducted incorrectly by combining Odds Ratios (OR) and Hazard
Ratios (HR), which may lead to misleading conclusions. Separate analyses should be performed
for studies using OR and those using HR.
7) The assessment of publication bias should be conducted separately for studies using HR and
those using OR, rather than across the total number of included studies, as they have different
effect sizes.
8) The discussion section should be revised. Simply presenting studies included in the meta-
analysis does not provide additional value to the manuscript.
9) The authors should compare their findings with studies evaluating adherence to the DASH
diet and its association with cancer risk or other health outcomes, such as diabetes mellitus
and hypertension. Additionally, they should explore potential molecular and pathophysiological
mechanisms underlying concordant or contradictory findings.
10) The limitations section should be expanded to include additional relevant limitations that
have not been addressed.
11) The authors should clarify the novel contributions of this review in comparison
to previously published reviews, specifically referring to the following studies:
[PMID: 31418286](https://pubmed.ncbi.nlm.nih.gov/31418286/) and [PMID: 32063407]
(https://pubmed.ncbi.nlm.nih.gov/32063407/).
Review for 10.1186/s12876-025-03942-8 (2025)

Title: Eosinophilic Esophagitis Patients Report Substantial Disease Burden Comparable to
More Systemic Immune-Mediated Diseases
Version: 3 Date: 06 Apr 2025
Reviewer's report:
The paper describes the disease-burden in a Swiss cohort of eosinophilic esophagitis as assessed
by patient-developed web-based questionnaire evaluating various domains of the quality of life
(leisure, social, travel) by comparison with a cohorts of patients with systemic immune-mediated
diseases, such inflammatory bowel disease (IBD), as systemic lupus erythematosus, systemic
scleroderma.
The main study finding was that perceived impairment in everyday life, particularly within
subdomains such as leisure, is substantial and comparable to that experienced by patients with
other immune-mediated disease states, including IBD.
The topic if of interest and the manuscript is generally well written.
There are some major methodological concerns
The web-based questionnaire distributed by national organisations may constitute a selection
bias favouring the enrolment of highly motivated patients with internet access.
Regarding response bias, given that the study is patient-generated, disease burden estimates may
be inflated.
There are, as the authors acknowledge, concerns about the validity of the questionnaire. A formal
validation is lacking and the definition of subdomains (such as leisure, social, travel) is not
accuracy.
Regarding study design an interesting comparison group would be the subgroup of patients with
scleroderma and oesophageal involvement.
From the statistical perspective, response rate within the cohorts is not thoroughly assessed. The
sample may not be representative of the whole cohort.
Moreover, when evaluating impairment scores across diseases adjustments for disease severity,
sex and age are not performed.
As the authors state among study execution limitation a low percentage of male SLE and SCC
took part in the study, making sex comparisons not accurate.
Review for 10.1186/s12876-025-03942-8 (2025)

Title: Eosinophilic Esophagitis Patients Report Substantial Disease Burden Comparable to
More Systemic Immune-Mediated Diseases
Version: 3 Date: 08 Apr 2025
Reviewer's report:
In this patient-initiated study, Theswet et al used a web-based questionnaire to assess quality
of life and disease-related impairment in Eosinophilic Esophagitis Patients compared to SSc,
SLE and IBD patients.
Among the 608 patients participated in the survey, EoE patients' perceived impairment in
everyday life appears to be comparable to that experienced by patients with other immune-
mediated disease states and worse among female EoE patients and those with a longer diagnostic
delay.
Overall, the manuscript is well written and the study well conducted.
Here are some comments:
1. The lack of formal validation of the questionnaire represents a major limitation for the
interpretation of data. A way to improve generazability would have been to use general QoL
questionnaires such as Sf-36 or the EuroQol.
2. Adding analysis of correlation between variables (general and within each group of patients)
would be helpful.
3. figures: Was a visual analogue scale (VAS) used or rather a numering rating scale (NRS)?
Please correct as appropriate.
Review for 10.1186/s12876-025-03806-1 (2025)

Title: Epidemiological Status of Family-Based Helicobacter pylori Infection in Yunnan
Province, China
Version: 2 Date: 22 Jan 2025
Reviewer:  Fernando P. Monroy
Reviewer's report:
The manuscript was well-written and easy to follow. Minor concerns are:
1) The manuscript is plagued with style errors.
2) A thorough English readthrough is needed to correct these mistakes. Some are minor, such
as a lack of space between words or a font of different sizes.
3) be consistent; italicize H. pylori throughout the manuscript.
4) The inclusion of limitations in the discussion section is important, but the authors should also
consider the specificity of the UBT in this section.
Review for 10.1186/s12876-025-03806-1 (2025)

Title: Epidemiological Status of Family-Based Helicobacter pylori Infection in Yunnan
Province, China
Version: 2 Date: 22 Jan 2025
Reviewer's report:
The article titled "Epidemiological Status of Family-Based Helicobacter pylori Infection in
Yunnan Province, China" explores the critical issue of Helicobacter pylori Infection in medicine.
In the paper, authors discuss an important issue -The current form of manuscript may be
acceptable with minor modifications and a point given below:
English language and style require editing, with some reformatting for grammatical mistakes.
H. pylori should be italicized in all text.
With Kind Regards
Review for 10.1186/s12876-025-03806-1 (2025)

Title: Epidemiological Status of Family-Based Helicobacter pylori Infection in Yunnan
Province, China
Version: 2 Date: 12 Feb 2025
Reviewer's report:
Title:
In the title, Helicobacter pylori should be italicized.
Abstract:
H. pylori should be italicized
Background:
Studying in a province cannot represent the whole country.
Introduction:
The name H. pylori needs correction throughout the manuscript.
Waeern should be corrected as Warren
Methods:
Ethical approval reference number is not provided.
Result:
What are minors? You mentioned about ethnic minority in this province however here it seems
subjects with younger ages. Clearly mention that.
General:
Bacterial name H. pylori must be corrected throughout the manuscript.
Minor grammatical errors must be addressed.
Review for 10.1186/s12876-025-03806-1 (2025)

Title: Epidemiological Status of Family-Based Helicobacter pylori Infection in Yunnan
Province, China
Version: 3 Date: 11 Mar 2025
Reviewer:  Fernando P. Monroy
Reviewer's report:
The manuscript is much improved; however, numerous punctuation and grammatical errors
remain.  I would encourage you to work with the editorial office to address them. On the other
hand, the information in the manuscript is clear and the graphs are well presented.
Review for 10.1186/s12876-025-03806-1 (2025)

Title: Epidemiological Status of Family-Based Helicobacter pylori Infection in Yunnan
Province, China
Version: 4 Date: 19 Mar 2025
Reviewer:  Fernando P. Monroy
Reviewer's report:
The mansucri[pt] is much improved. In the current version, punctuation, and spaces are still
evident. Nevertheless, the editorial office can easily resolve this issue.
Review for 10.1186/s12876-025-03903-1 (2025)

Title: Characteristics of serum bile acid profiles among individuals with metabolic dysfunction-
associated steatotic liver disease
Version: 0 Date: 23 Feb 2025
Reviewer's report:
1. those with serious heart, brain, lung, kidney, and other systemic diseases – this is a vague
expression. Exclusion criteria should be stringent.
2. Please use inclusion criteria for NAFLD/MAFLD/MASLD as defined by AASLD/APASL/
EASL
3. The patients were instructed to adhere to a light diet and refrain from smoking and drinking
the day before sampling to minimize metabolic fluctuations.  – Please cite appropriate reference
in support of this statement.
4. All experimental data were analyzed using IBM SPSS Statistics for Windows, version 26.0
– Please mention full company details, country and city.
5. It is noteworthy that the levels of body mass index (BMI), ALT, TG, TC, and FBG were
markedly elevated in the MAFLD group compared to the healthy individuals (P = 0.008, P =
 0.005, P = 0.005, P = 0.006, P < 0.001). – What is noteworthy here? It is entirely expected.
Suggest authors to remove ‘noteworthy’.
6. In some section, we compared the data for each of the two groups. Therefore, the significance
level P = 0.05 was divided by two, which provides a significance level corrected for multiple
testing: P = 0.025. – Is this statistically appropriate? P value of 0.025 is used when doing a one-
tailed test. A one-tailed test is appropriate if the estimated value may depart from the reference
value in only one direction, left or right, but not both. Please clarify.
7. The analysis encompassed a total of 264 participants, including 215 participants diagnosed
with MAFLD and 49 controls. – Were the controls matched for age, sex and geography? It is
very important to have matched controls in such studies as metabolic parameters can vary widely
depending upon age, sex, etc.
8. What proportion of MAFLD subjects were overweight/obese or had normal BMI? Were
there any MAFLD subjects with normal BMI (lean NAFLD)? Similarly, what proportion of the
controls were overweight/obese or had normal BMI? Were these comparable between the two
groups? These details are very pertinent.
9. ALT levels, defined as normal (# 50 U/L for males and # 40 U/L for females) and elevated (>
 50 U/L for males and > 40 U/L for females), - What is the evidence for this cut-off? Is it based
on any guidelines, consensus or strong evidence? Please clarify.
10. What is the implication of elevated bile acid levels in MAFLD? Please discuss the therapeutic
implications. Despite these findings, molecules like obeticholic acid have failed to cause
significant headway. Are elevated bile acid levels the cause or effect of MAFLD? If these are
offshoots of hepatic steatosis, what therapeutic implication might this have? Kindly discuss.
Review for 10.1186/s12876-025-03903-1 (2025)

Title: Characteristics of serum bile acid profiles among individuals with metabolic dysfunction-
associated steatotic liver disease
Version: 2 Date: 28 Mar 2025
Reviewer:  Akira Honda
Reviewer's report:
The authors provided supplemental material but insufficient information for other researchers
to repeat the bile acid analysis. How much serum was used, and how was it processed? What
were the composition of the UPLC mobile phases, the column name used, the monitoring ion
of each bile acid, etc.?
Review for 10.1186/s12876-025-03948-2 (2025)

Title: Global burden of colon and rectal cancer and attributable risk factors in 204 countries and
territories from 1990 to 2021
Version: 0 Date: 19 Feb 2025
Reviewer:  Sina Azadnajafabad
Reviewer's report:
Thanks for the chance to review this study on the global burden of colorectal cancer and
attributable risk factors using the recent GBD 2021 data. The findings of this research is mostly
consistent with previous publications like the ones on the same topic using the GBD 2019 data.
I would like to ask authors to expand their analysis framework to address the emerging trends
in the colorectal cancer epidemiology to make this effort beneficial. Otherwise, publishing the
findings would not benefit the audience. See below for my comments and suggestions.
1. Recent trends show different patterns of colorectal cancer incidence and mortality in younger
population (age < 50 y) compared to older population. So, stratifying the analysis for this issue
could add to the research value.
2. Also, the recent diverging patterns of colorectal cancer in men and women necessitates to
focus more on the sex-specific results rather than overall estimates.
3. Considering the emerging concept of birth cohort effects in the incidence and mortality of
several cancer globally, it is highly suggested to add the age-period-cohort analysis to the study
methods and results.
4. Regarding the use of the World Bank’s income categorizations, it is not clear if authors
retrieved the data separately or just used the results extracted for WB income levels from GBD
data. In case of separate data extraction, authors need to mention the year for leveling and the
reason for separate data extraction.
5. Discussion: this section adds nothing specific to the body of literature. If authors consider the
major changes in the methods there might be some specific points to discuss in this section.
Review for 10.1186/s12876-025-03948-2 (2025)

Title: Global burden of colon and rectal cancer and attributable risk factors in 204 countries and
territories from 1990 to 2021
Version: 0 Date: 03 Mar 2025
Reviewer's report:
This manuscript leverages the Global Burden of Disease (GBD) 2021 data to conduct a
thorough evaluation of global, regional, and country-specific trends in colon and rectal cancers
(CRCs). The authors report on incidence, prevalence, mortality, and disability-adjusted life
years (DALYs), then delineate how multiple risk factors—such as high red meat consumption,
obesity, and insufficient calcium intake—contribute to CRC burdens across different World
Bank income regions. Notably, the authors observe a decline in the global age-standardized
DALY rate (ASDR) and mortality rate (ASMR) for CRC from 1990 to 2021, although the age-
standardized incidence rate (ASIR) slightly increased. Importantly, there is substantial regional
heterogeneity: high-income regions demonstrate progress in decreasing mortality and DALYs
while still bearing the highest CRC burden. By contrasting these diverse patterns, the manuscript
underscores the role of socioeconomic factors and lifestyle exposures in driving CRC outcomes.
Overall, this manuscript offers compelling analysis and valuable insights for global health
stakeholders. Once the following points are addressed in a revision, it will be well placed for
publication:
Please provide more detailed information on how UIs and CIs were calculated. Indicate the
statistical methodologies, software, or models used to generate these intervals, and outline any
underlying assumptions (e.g., bootstrapping or Monte Carlo simulations).
Some terms, such as “women” versus “female,” appear inconsistently throughout the
manuscript. Incorporate standard language (e.g., “women” or “males”/“females”) and apply it
uniformly to maintain clarity and professionalism.
While the manuscript marks a significant contribution to understanding CRC burdens,
further discussion on the public health implications of the results would be beneficial. This
would include how policymakers might leverage these findings to guide cancer prevention
measures, screening programs, dietary guidelines, and educational campaigns within varying
socioeconomic contexts.
Review for 10.1186/s12876-025-03801-6 (2025)

Title: The risk factors affecting effect of extracorporeal shock wave lithotripsy for pancreatic
duct stones
Version: 2 Date: 05 Feb 2025
Reviewer:  Ahmed Reda
Reviewer's report:
Thank you for your work
Comments:
The idea of the research should be revised as:
1-ESWL for common bile duct stones carries many risks:
a. Obstruction of the common bile duct with its sequences.
b. The risk of hematoma due to the fragility of the tissues.
c. There is a need for further maneuvers if obstruction occurs.
2-The authors didn't discuss the complications in detail.
3- Language checks and improvement is needed.
Review for 10.1186/s12876-025-03801-6 (2025)

Title: The risk factors affecting effect of extracorporeal shock wave lithotripsy for pancreatic
duct stones
Version: 2 Date: 06 Feb 2025
Reviewer's report:
This article investigates the risk factors for SIRS occurring during RIRS for solitary kidneys.
However, the study design and content have significant flaws, and therefore, the article is not
recommended for publication. The specific issues are as follows:
The study is retrospective with a small sample size.
The definition of SIRS used in this study is outdated.
Many recent studies have already explored the risk factors for infectious complications during
RIRS. This study does not provide any new insights or findings.
The introduction of the flexible distal aspiration sheath has significantly improved the outcomes
of RIRS. However, this study is still based on the traditional ureteral access sheath, making its
content and conclusions outdated.
Review for 10.1186/s12876-025-03801-6 (2025)

Title: The risk factors affecting effect of extracorporeal shock wave lithotripsy for pancreatic
duct stones
Version: 2 Date: 10 Feb 2025
Reviewer's report:
Dear Author
I reviewed the article
I have some questions
How did you decise SWL for pancreatic duct stones? Did SWL have an indications for this
stone?
The ESWL abbreviation should be revised as SWL
How did you inform patients?
Kind Regards
Review for 10.1186/s12876-025-03888-x (2025)

Title: Triglyceride glucose waist circumference and Non alcoholic fatty liver disease: a
systematic review and meta analysis
Version: 0 Date: 25 Feb 2025
Reviewer's report:
Dear Authors,
Thank you for your submission. The article demonstrates a comprehensive analysis, and the
methodology is well-structured. However, some aspects of the manuscript require attention to
enhance its clarity and overall impact.
1. In the introduction section, it is imperative to include more recent studies to mention the
prevalence and burden of NAFLD. A recent meta-analysis published in 2024 offers updated data
on the global prevalence of NAFLD.
2. Although you’ve outlined the potential mechanisms linking TyG-WC, insulin resistance, and
NAFLD, a concise illustration would greatly improve the clarity of these concepts.
3. In the Figure 5, the terms “control” and “experimental” are not appropriate for this study’s
design. I advise revising these labels to better align with the study’s methodology.
Review for 10.1186/s12876-025-03888-x (2025)

Title: Triglyceride glucose waist circumference and Non alcoholic fatty liver disease: a
systematic review and meta analysis
Version: 1 Date: 30 Mar 2025
Reviewer's report:
Dear authors,
I would like to thank you for the opportunity to review the modified manuscript entitled
"Triglyceride glucose waist circumference and Non-alcoholic fatty liver disease: a systematic
review and meta-analysis."
After reviewing the modified manuscript in details, There are some suggestions for authors to
improve readability and quality:
1- The article mentioned conducting additional sensitivity analyses, including meta-regression
of potential confounding variables (NAFLD diagnostic methods, population types, and study
design) to elucidate their role as not the main sources of heterogeneity, and claimed that were
presented at Supplementary Table 3. The mentioned table must be provided since it was not
uploaded in the article-related supplementary files.
2- I think the authors put their efforts in modifying the labels of Figure 5 for better reflecting
the outcome categories in the meta-analysis(“low” vs. “high”), but it seems that the uploaded
version of the figure is corrupted and the corrected copy must be uploaded to support the study
claims.
Otherwise, the authors have adhered to every comments / suggestions being provided in the peer
review, and justifications for these changes have been discussed in the modified manuscript.
Review for 10.1186/s12876-025-03888-x (2025)

Title: Triglyceride glucose waist circumference and Non alcoholic fatty liver disease: a
systematic review and meta analysis
Version: 1 Date: 30 Mar 2025
Reviewer's report:
Dear Authors,
Thank you for resubmitting your manuscript  for further review. I appreciate the revisions made
and the detailed responses to my previous comments. Below is my assessment of the revised
manuscript:
Updated Prevalence and Burden of NAFLD
I acknowledge that the prevalence of NAFLD has been updated in the Introduction section. The
manuscript now offers a more comprehensive and updated context.
Thank you for linking the TyG-WC index to insulin resistance  and explaining its connection
to the development of NAFLD in the Discussion. However, to make these relationships clearer,
I suggest incorporating a visual illustration that maps out the pathways from TyG index to IR,
and then from IR to the progression of NAFLD. Many studies have explored these pathways
and you can use them.
Also you can mention the role of obesity, particularly waist circumference, in this process. WC
is a key indicator of visceral fat and has a well-established link to IR and NAFLD progression
and you can add this information in your illustration.
Figure 5 Labels
Thank you for updating Figure 5. However, I was unable to open the new file. Please resend
it for review.
Overall, the revisions have improved the clarity and quality of the manuscript. However, I
suggest the addition of a visual mechanism illustration, as discussed above, to further strengthen
the paper.
Review for 10.1186/s12876-025-03888-x (2025)

Title: Triglyceride glucose waist circumference and Non alcoholic fatty liver disease: a
systematic review and meta analysis
Version: 2 Date: 09 Apr 2025
Reviewer's report:
I would like to thank the authors for their excellent work and for submitting this manuscript.
Since the authors have submitted the recommended modifications, as well provided a
comprehensive and well-supported argument, leading to an enhancement in clear presentation
of manuscript concepts and outcomes to make a significant contribution to the field.
Thus, I am pleased to recommend this manuscript for publication.
Review for 10.1186/s12876-025-03891-2 (2025)

Title: A clinical predictive score of high liver iron content in metabolic hyperferritinemia; a
retrospective cohort pilot study
Version: 2 Date: 01 Mar 2025
Reviewer's report:
this idea is very good to differentiate subject need for MRI liver for iron quantification which is
advanced imaging technique, this score will  has good beneficial   clinical impact
Review for 10.1186/s12876-025-03891-2 (2025)

Title: A clinical predictive score of high liver iron content in metabolic hyperferritinemia; a
retrospective cohort pilot study
Version: 2 Date: 06 Mar 2025
Reviewer:  Tomas Koller
Reviewer's report:
Dear editor, I read with interest the manuscript entitled "A clinical predictive score of high liver
iron content in metabolic hyperferritinemia; a retrospective cohort pilot study "
The topic is up-to-date, and the study is nicely presented with a sound introduction, methods,
and results. The clinical application of the results is somewhat limited, but since very few studies
have addressed the prediction of liver iron overload in DIOS, it is certainly of value to clinicians,
particularly hepatologists. I have no major comments or issues, but I have a few questions.
1. The threshold for DIOS has been set at 74 umol/g (citation 20). What percentage of the cohort
had grade 3 DIOS according to this cut-off? The authors do not explain in detail what was the
rationale for this value. Was there any evidence that iron overload beyond this value is toxic
for the liver?  If so, it would be clinically useful to identify all patients with DIOS, not only
those with severe iron overload beyond 100umol/g. Were the authors considering the predictive
model for this DIOS threshold?
2. The predictive score is not very granular as seen in the ROC curve, so my question is did the
authors consider a more granular means of creating the predictive score (values for ferritin and
transferrin saturation are numerical), for example, a logit equation with probability?
3. Did the authors have a chance to add some fibroscan parameters (stiffness, CAP) to the
predictive model, I imagine that these patients had these exams done at some point.
4. I do not see any liver tests or GGT in the Tables, those should have been available since they
are listed in the data collection, were they tested as predictors of DIOS?
5. It is interesting to see some difference in dyslipidemia between the groups, but not in the
actual triglycerides or HDL. How do the authors explain this finding? Did they consider therapy
for dyslipidemia as a possible cause?
6. From the studied cohort with a follow-up of over  6 years, did the authors have a chance to
look at outcomes in terms of morbidity and mortality according to iron overload?
Review for 10.1186/s12876-025-03891-2 (2025)

Title: A clinical predictive score of high liver iron content in metabolic hyperferritinemia; a
retrospective cohort pilot study
Version: 2 Date: 07 Mar 2025
Reviewer's report:
The paper reports on using ROC curve analysis to improve the ability of MR Liver Iron
estimation to predict hepatic iron overload.  The patient profile is a large group of French patients
who have been diagnosed with dysmetabolic syndrome which was first described in France.
The liver histology differs from C282Y linked hemochromatosis and it has not been established
that venesection improves outcomes.
It would be expected that a positive family history, high ferritin and transferrin saturation would
be correlated with liver iron concentration.  The ROC analysis provides a statistical proof
although the key variable the area under the curve (AOC) gives only an acceptable result, a AOC
> 0.8 would have been preferred.
This use of scoring systems are rarely used by physicians.  In some studies, an app is created to
simplify the calculations and interpretation.   In this study, the analysis would likely be done by
the radiologist and thus the paper may be better suited to a short report in an imaging journal.
The impact of the study is low because the need for venesection is not clear and some patients
get worse with venesection.
The references should include a large study from France by LeGac et al that demonstrated that
most French patients undergoing venesections for iron overload, do not have iron overload.
Ailiment Pharmacol Ther 2022 doi: 10.1111/apt.16775 .
Review for 10.1186/s12876-025-03924-w (2025)

Title: The Role of C-reactive protein to lymphocyte ratio in NAFLD and  Mortality Among
NAFLD Patients
Version: 2 Date: 13 Feb 2025
Reviewer's report:
Dear Authors,
Thank you for your submission. While your study addresses an interesting topic, we have
several concerns regarding its novelty, methodology, and statistical robustness. Given the
existing research on the association between CLR and NAFLD, the study lacks sufficient
originality. Additionally, the use of different diagnostic criteria across NHANES survey years
raises concerns about potential misclassification bias. The statistical effect sizes are relatively
small, and the clinical significance of the findings remains uncertain.
Due to these limitations, we are unable to recommend this manuscript for publication. We
appreciate your efforts and encourage you to refine your study, addressing these concerns in
future research.
Best regards,
Reviewer
Review for 10.1186/s12876-025-03924-w (2025)

Title: The Role of C-reactive protein to lymphocyte ratio in NAFLD and  Mortality Among
NAFLD Patients
Version: 2 Date: 16 Feb 2025
Reviewer's report:
1. It is recommended to avoid abbreviations in the title. Please replace "CLR" with its complete
form, "C-reactive protein to lymphocyte ratio."
2. In the results section of the abstract, the term "Model 3" is used without prior explanation.
Please clarify what "Model 3" refers to.
3. Specify the duration of follow-up for the all-cause mortality outcome. Additionally, provide
the number of NAFLD participants who died during the follow-up period.
4. Ensure consistency in reporting statistical values. P-values are presented with three decimal
places; all other values, such as confidence intervals, should also be noted with three decimal
places.
5. Cholesterol, triglycerides, and HDL are reported, but LDL is notably absent. Please clarify
why LDL was not included. Additionally, it would be beneficial to include hepatic biomarkers
such as AST and ALT.
6. The authors do not account for critical comorbidities such as heart failure or stroke. If possible,
please consider including these conditions in the medical history covariates.
7. While all-cause mortality is assessed, it would strengthen the study to determine specific
causes of death among NAFLD patients and perform subgroup analyses based on these causes.
8. Including Kaplan-Meier survival curves for all-cause mortality, stratified by CLR quartiles,
in NAFLD patients would enhance the study.
9. Abbreviations such as hazard ratio (HR) are introduced multiple times. Please ensure that
each abbreviation is defined once upon first use.
10. In Figure 1, it is stated that 1849 participants were excluded from 5921 participants with
complete data, leaving 4027 participants. However, 5921 minus 1849 equals 4072, not 4027.
Please correct this discrepancy. Additionally, all abbreviations used in Figure 1 should be
defined.
11. The title of Figure 3 uses the abbreviation "CLP," which seems incorrect. Please revise it
to "CLR."
12. Machine learning methods such as Random Forest and K-Nearest Neighbors are mentioned
in the discussion and in the abbreviation section (line 261). However, these methods are not
described in the methods or results sections. Please provide details on whether these methods
are employed.
13. In Table 1, Clarify if the "high cholesterol" classification is based on a specific cutoff. Correct
the misspelling of "Diabetes."
14. Although the study aims to highlight CLR as a significant biomarker in NAFLD patients,
it would be more robust to compare CLR with other established biomarkers for NAFLD in the
discussion section.
Review for 10.1186/s12876-025-03924-w (2025)

Title: The Role of C-reactive protein to lymphocyte ratio in NAFLD and  Mortality Among
NAFLD Patients
Version: 4 Date: 05 Apr 2025
Reviewer's report:
The authors have adequately addressed all comments and concerns raised. The revisions are
appropriate and clearly improve the quality and clarity of the manuscript.
Review for 10.1186/s12876-025-03915-x (2025)

Title: Modified Triglyceride-Glucose Indices as Novel Predictors of Metabolic Dysfunction-
associated Fatty Liver Disease in US Adolescents: A Nationally Representative Study from
NHANES 2017-2020
Version: 1 Date: 14 Mar 2025
Reviewer's report:
Thank you for  involved me in the revision process of the present manuscript. This manuscript
is well written, but lacks of a true novelty and suffer of many issues:
1. The study population consists of a relatively small sample size, which may not be
representative of the broader adolescent population. At the same time, the demographic
composition, with a predominance of Non-Hispanic White participants, limits the
generalizability of the findings to diverse racial and ethnic groups.
2. The confounding factors were insufficiently adjusted in the final model, raising concerns
about potential residual confounding in the observed associations.
3. The manuscript highlights a significant association between TyG indices and CAP; however,
the disappearance of significance for the TyG index and TyG-BMI in Model 3 contradicts the
earlier conclusions.
4. While the association between TyG-related indices and NAFLD has been explored in previous
studies, this manuscript does not provide substantial novel insights beyond existing literature.
The clinical implications of the findings are not well-articulated, and the practical utility of
modified TyG indices in adolescent NAFLD risk stratification remains unclear.
5. The new MASLD nomenclature was not adopted. NAFLD nomenclature has been changed
at the end of 2023.
Review for 10.1186/s12876-025-03915-x (2025)

Title: Modified Triglyceride-Glucose Indices as Novel Predictors of Metabolic Dysfunction-
associated Fatty Liver Disease in US Adolescents: A Nationally Representative Study from
NHANES 2017-2020
Version: 1 Date: 27 Mar 2025
Reviewer's report:
This manuscript presents an insightful study investigating the predictive value of modified
triglyceride-glucose (TyG) indices for non-alcoholic fatty liver disease (NAFLD) in adolescents
using NHANES data. The study is well-structured and addresses a clinically relevant topic.
However, several aspects require revision and clarification to enhance the manuscript's scientific
rigor and overall quality.
- The terminology for NAFLD has recently been updated to metabolic dysfunction-associated
steatotic liver disease (MASLD). It is recommended that the authors adopt this revised
nomenclature while considering a subgroup analysis to compare findings between MASLD and
the previous NAFLD definition.
Methodological Considerations:
- The methods section mentions liver stiffness measurement, yet the manuscript does not report
these results. Please include the liver fibrosis data and analyze the association between TyG
indices and fibrosis severity.
- To comprehensively assess the predictive accuracy of the TyG indices for identifying NAFLD/
MASLD, the area under the receiver operating characteristic curve (AUROC) should be
calculated. Please incorporate AUROC analysis into the statistical methodology and report these
findings.
- Clarify the time interval between the CAP/LSM assessments and blood sample collection used
for calculating the TyG indices. If there is a significant delay between these assessments, discuss
its potential impact on the study findings.
Discussion:
- Compare the study results with previous literature utilizing NAFLD, MAFLD, and MASLD
diagnostic criteria, and discuss any discrepancies arising from the different classification
systems.
- Contextualize the AUROC values obtained in this study by comparing them with other
commonly used non-invasive biomarkers and scoring systems.
- Discuss whether there are age-related differences in the diagnostic performance of these indices
between adolescents and adults.
- Elaborate on the clinical implications of the findings, particularly their potential utility in
screening or early identification of NAFLD/MASLD in adolescents.
By addressing these points, the manuscript will be significantly strengthened, providing greater
clarity and impact.