JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-03976-y (2025)

Title: Clinical Challenges and Patient Experiences in Early-Onset Colorectal Cancer: Insights
from Seven European Countries
Version: 4 Date: 12 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-A high level of educational attainment (42 of 47 had university degrees) may limit
generalizability to broader, less educated populations.
-Underrepresentation of patients under 30 (despite being a key risk group) could skew insights
toward older “young adults” (35–49).
-Although participants ranged from Stage II to IV, the data were not stratified by stage, which
may obscure important differences in experiences and care needs.
-Although translation was carefully managed, translation bias is always a risk in qualitative
research. Some emotional nuance may be lost or altered in non-English transcripts.
-Potential cultural expressions may not be fully preserved, despite researchers’ efforts to address
cross-cultural variation.
-Thematic analysis is rich, but no quantitative measures or standardized patient-reported
outcomes were included to complement the qualitative findings.
Limits the ability to compare the severity or prevalence of issues across countries or subgroups.
-While the study discusses systemic healthcare barriers, it lacks a detailed analysis of health
policy structures, budgets, or systemic reforms.
-Policy recommendations are implied, but not fully fleshed out or actionable.
-The discussion could benefit from anchoring in a stronger conceptual or theoretical framework
(e.g., patient-centered care models, and health equity theories).
-This would help connect findings to broader discussions in health policy and public health.
Some repetition across sections (e.g., fatigue and gender issues are revisited multiple times)
could be tightened for better clarity and impact.
-While the study highlights underrepresentation, there’s minimal discussion of socioeconomic,
racial, or ethnic diversity, which could limit the applicability of findings to marginalized
populations.
-While stage-specific differences are acknowledged in the Limitations, the lack of subgroup
analysis (by stage, gender, country) feels like a missed opportunity—especially given the rich
qualitative material.
-The policy recommendations are strong but could be better prioritized (e.g., short-term vs. long-
term interventions) or supported by more specific implementation strategies.
Some claims (like the role of stress or fatigue as a red flag) are intriguing but lack sufficient
empirical backing in this study.
-These should be more clearly flagged as hypotheses or emerging areas rather than firm
conclusions.
Review for 10.1186/s12876-025-03946-4 (2025)

Title: Machine learning for predicting all-cause mortality of metabolic dysfunction-associated
fatty liver disease: a longitudinal study based on NHANES
Version: 1 Date: 17 Mar 2025
Reviewer's report:
This study has several strengths that enhance its significance and reliability. First, it leverages
a well-established, nationally representative dataset (NHANES III) with long-term follow-
up, ensuring a robust and comprehensive analysis of MAFLD-related mortality. Second,
by incorporating multiple machine learning models (Coxnet, RSF, GBS), the study allows
for a comparative evaluation of predictive performance, ensuring that the best-performing
model is identified. Third, the inclusion of diverse predictors—ranging from demographic and
behavioral factors to laboratory indicators—enhances the model’s ability to capture complex
risk relationships. Fourth, the use of interpretable machine learning methods, along with
traditional survival analyses, provides valuable clinical insights rather than treating the model
as a black box. Finally, the study’s findings offer practical implications for community health
interventions by identifying modifiable risk factors, which could improve patient outcomes and
guide personalized treatment strategies.
However, there are some limitations to consider. First, while machine learning models
demonstrated strong predictive capabilities, their real-world applicability depends on external
validation in independent cohorts, which was not performed in this study. Second, the reliance on
NHANES III data, although valuable, may not fully capture recent shifts in MAFLD diagnosis,
management, or treatment strategies. Third, despite careful feature selection, unmeasured
confounders such as genetic predisposition, medication use, and gut microbiota composition
may still influence all-cause mortality in MAFLD patients. Fourth, while the study establishes
associations between risk factors and mortality, causality cannot be inferred due to the
observational nature of the data. Lastly, the predictive models require further calibration and
refinement before they can be seamlessly integrated into clinical practice, highlighting the need
for additional prospective studies to confirm their utility.
Consider some or all of these articles to help with weaknesses identified in this review, focusing
on the methods:
https://onlinelibrary.wiley.com/doi/full/10.1111/jch.14745
https://www.elsevier.es/en-revista-annals-hepatology-16-avance-resumen-accurate-prediction-
all-cause-mortality-in-S1665268124003223
https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0281922
https://www.nature.com/articles/s41514-023-00127-z
https://journals.plos.org/plosone/article?id=10.1371/journal.pone.0282622
https://pmc.ncbi.nlm.nih.gov/articles/PMC9099391/
https://www.sciencedirect.com/science/article/pii/S2475299123212512
Review for 10.1186/s12876-025-03946-4 (2025)

Title: Machine learning for predicting all-cause mortality of metabolic dysfunction-associated
fatty liver disease: a longitudinal study based on NHANES
Version: 1 Date: 25 Mar 2025
Reviewer's report:
1. A dedicated literature review or related works section should be added to review similar
studies relevant to this manuscript.
2. The dataset's degree of skewness and kurtosis should be reported.
3. Methods for balancing the dataset should be considered to equalize the number of samples
across different classes.
4. Given the lower mortality rate in the dataset, was any technique other than 10-fold cross-
validation used to mitigate potential bias and error in the machine learning models? Please
clarify.
5. A detailed description of the machine learning models used in this study should be provided.
6. Additional evaluation metrics, such as F1-score, NPV, PPV, and accuracy, should be
incorporated to provide a more comprehensive assessment of model performance.
7. The discussion section requires further elaboration on the application and effectiveness
of machine learning models in this field. The findings should be analyzed in greater
depth, incorporating perspectives from physicians, and the results should be compared more
comprehensively with similar studies.
8. The advantages and disadvantages of the proposed method should be explicitly stated in the
conclusion section.
9. Since this manuscript primarily employs common machine learning algorithms for predicting
all-cause mortality in metabolic dysfunction-associated fatty liver disease, its technological
innovation is limited. Additional machine learning and deep learning models, such as support
vector machines, k-nearest neighbors, multilayer perception, etc., are recommended to enhance
novelty. Moreover, metaheuristic algorithms like the bat and genetic algorithms could be applied
for feature selection, with the results compared to the current findings.
Review for 10.1186/s12876-025-03936-6 (2025)

Title: INTRAVENOUS SEDATION DURING ESOPHAGOGASTRODUODENOSCOPY IS
ASSOCIATED WITH A REDUCED RISK OF MISSED GASTRIC CANCER
Version: 1 Date: 09 Mar 2025
Reviewer's report:
•  This is a small, single-center retrospective study.
•  The Introduction and Discussion sections are too long.
•  The study includes patients with lymphoma and GIST, but their risk of developing
metachronous cancer differs from that of gastric cancer.
•  It is unclear why the study population was limited to patients with tumors identified during
endoscopy. There is a mismatch between the general aim of investigating factors contributing
to the missed diagnosis of gastric cancer and the specific study design and objectives.
•  Table 2 is insufficient. The results of both univariate and multivariate analyses regarding
predictors of metachronous gastric cancer should be included.
•  Based on the current findings, concluding that EGD without sedation is a risk factor for
metachronous gastric cancer is an overstatement. This is because there are baseline differences
between patients who underwent EGD with and without sedation, and the study is not a
randomized controlled trial.
•  Even if Helicobacter pylori infection status could not be assessed, the degree of gastric mucosal
atrophy should have been evaluated as an important factor potentially associated with gastric
cancer development.
Review for 10.1186/s12876-025-03936-6 (2025)

Title: INTRAVENOUS SEDATION DURING ESOPHAGOGASTRODUODENOSCOPY IS
ASSOCIATED WITH A REDUCED RISK OF MISSED GASTRIC CANCER
Version: 2 Date: 14 Apr 2025
Reviewer's report:
The paper has been appropriately revised in accordance with the reviewers' comments.
Review for 10.1186/s12876-025-03929-5 (2025)

Title: Changes in microbial and metabolic profiles of mice fed with long-term high salt diet
Version: 2 Date: 01 Aug 2024
Reviewer's report:
In this study, the authors investigated the changes in microbial and metabolic profiles of mice fed
with long-term high salt diet. Generally, the study was well designed and the results are good.
Revisions are recommended for further publication.
(1) In the results section, the authors just described the composition of gut microbiota,
metabolites and their associations. They did not provide any verification results. It will be very
good if they provide RT-PCR results or germ-free mice to confirm the bacteria to be interested.
(2) What are the innovations in this study compared with previous studies? Please describe it
somewhere in the text.
Review for 10.1186/s12876-025-03929-5 (2025)

Title: Changes in microbial and metabolic profiles of mice fed with long-term high salt diet
Version: 2 Date: 22 Aug 2024
Reviewer's report:
The manuscript titled "Changes in Microbial and Metabolic Profiles of Mice Fed a Long-Term
High Salt Diet," authored by Dini Lin et al., describes a model where mice are fed a long-
term high-salt diet (HSD). The study explores the effects of this diet on growth performance,
serum adipocytokines, and the composition and metabolites of fecal microbiota. The manuscript
is generally well-written and presented, with a methodology that is clearly detailed, ensuring
replicability. All of the figures are well generated and easy to understand. To further improve the
quality of your submission, I recommend a thorough proofreading to enhance language clarity
and precision. I also want to recommend the authors to use qiime 2 instead of qiime 1 as qiime
2 emphasizes data provenance by maintaining detailed records of all data transformations and
analyses.
Review for 10.1186/s12876-025-03929-5 (2025)

Title: Changes in microbial and metabolic profiles of mice fed with long-term high salt diet
Version: 2 Date: 26 Aug 2024
Reviewer:  Petia Kovatcheva-Datchary
Reviewer's report:
In the current manuscript the authors present data from animal intervention with high salt diet
content vs normal salt diet.
In general, the physiological observation related to the post effect of the high salt diet on the
mice metabolism is not unexpected, considering the effect high salt content brings to human.
However, it looks like here the novelty should be focused also not only on the long treatment
but also the analysis related to the gut microbiota and metabolites.
While this is interesting for the reviewer is unclear how such big conclusions and a whole paper
can be made only with 8 mice (4 mice per group). Therefore, the data need to be supported by
more mice, otherwise the study is very immature and inconclusive. Also, information related to
the housing of the mice (single per cage or a cage per group) is missing.
Further, the authors discus about changes in the gut microbiota, but what are the time dependent
changes in the microbiome during this high salt intervention.
Further, the approach of performing fecal metabolomics is very good, but what about the
metabolite’s levels in serum. This will be much more relevant considering the impact of the long
treatment to the host metabolism.
Finally, the statistics related to the correlation analysis needs more clear justification and
explanation.
Specific comments: In the material part of the abstract is indicated that animals were fed 22
weeks high salt diet and then feces and fat was collected, what about serum? Also, the host
characterization was done up to 30 weeks. Explanation for this is missing.
Please remove “gut” at line 24, the word “feces” is enough to explain the origin of the samples.
Review for 10.1186/s12876-025-03929-5 (2025)

Title: Changes in microbial and metabolic profiles of mice fed with long-term high salt diet
Version: 3 Date: 27 Sep 2024
Reviewer:  Petia Kovatcheva-Datchary
Reviewer's report:
The authors did some changes in the text, but this barely addresses the reviewer comments.
Still the big limitation is that in each group only 4 mice are included. Most probably mice were
housed each group in a cage, which suggests also that the cage effect lowers the power of the
data.
Furthermore, it is unclear why the contact information for the third corresponding author: Dr.
Xianen Huang is not included in the part for Corresponding Authors?
Review for 10.1186/s12876-025-03961-5 (2025)

Title: Surface Area Outcomes in EUS-Guided Liver Biopsy: A Comparative Study of Franseen
and Fork-tip Needles
Version: 2 Date: 23 Jan 2025
Reviewer's report:
I agree with the authors that reliance on total specimen length (TSL) is a limitation, and length
of the longest piece is probably better.  However, it is not clear to me why the “surface area”
is a better metric than, for example, length of the longest piece (LLP), or even total specimen
length. The surface area is closer to TSL than LLP and as such, has the same limitations as TSL.
The surface area is basically 2 times the specimen length, with a little more added on the ends.
So again, I am not sure of the advantage of surface area.
The use of whole slide imaging (ESI) is not a novel approach; it has been used extensive in
most of the prospective randomized studies comparing needle types and sizes, wet vs dry, and
number of passes.
It is interesting that the authors used “portal tracts” and not “complete portal tracts”, which has
been the standard in the literature on this subject. Is there a reason this was done?  This makes
the results harder to compare with portal triad data already in the literature.
It does not appear that a power analysis was done to understand how many patients would be
needed in each arm of the study.  As a result, it is not possible compare the two needles in terms
of adequacy or efficacy.
Figure 1 legend.  The description of the image is for the left pane only; the right panel is Doppler
and this is not indicated in the legend.  In any case, you probably only need a single image,
not both.
Review for 10.1186/s12876-025-03961-5 (2025)

Title: Surface Area Outcomes in EUS-Guided Liver Biopsy: A Comparative Study of Franseen
and Fork-tip Needles
Version: 2 Date: 06 Feb 2025
Reviewer's report:
1. According to the text (Results section, paragraph 2), the total hepatic tissue area in the two
groups was reported as an average of 22.0 mm² (range: 0.1–49.7 mm²) and 22.6 mm² (range:
7.5–47.8 mm²). However, in Table 3, the total hepatic tissue area in the two groups is presented
as median (IQR) 22.0 (0.1–49.7) vs. 22.6 (7.5–47.8). Since the range and IQR are identical,
could you please confirm this? The same issue appears to exist in the maximum hepatic tissue
area, total number of portal tracts, and other related variables.
2. How is the liver surface area defined? Are blood clots or adipose tissue within or surrounding
the tissue core included in the measurement? Was the measurement performed manually or
automatically?
3. How was the final diagnosis established? For example, in the Franseen-Tip group, three
patients (15%) were diagnosed with non-specific inflammatory changes. Would obtaining a
larger tissue sample have led to a more definitive diagnosis?
4. In the Methods section, the authors mentioned that the slow-pull technique was used for
the third biopsy when there was inadequate tissue yield or significant blood contamination in
the samples after the first two biopsies. How was 'inadequate tissue yield' defined? Was it
determined by ROSE or MOSE?
Review for 10.1186/s12876-025-03961-5 (2025)

Title: Surface Area Outcomes in EUS-Guided Liver Biopsy: A Comparative Study of Franseen
and Fork-tip Needles
Version: 4 Date: 01 Mar 2025
Reviewer's report:
1. In reference 19, the original MOSE study used MVC #4 mm as a criterion for specimen
adequacy. Did your study apply the same cut-off criteria?
2. Your study presents conflicting results compared to Nieto et al. (Ref. 23), possibly due to
differences in assessment methods (TSL vs. WSI). However, since total specimen length should
positively correlate with total tissue volume, would the conflict persist if your specimens were
measured using TSL? If discrepancies remain, please explain the possible reasons.
3. According to Table 3 and Figure 3, the median total hepatic tissue area and the maximum
hepatic tissue area per pass were different. However, in table 4, the unadjusted odds ratios (95%
CI) for sex, BMI, fibrotic stage, and MASLD were identical for both the total hepatic tissue area
and the maximum hepatic tissue area per pass. Please confirm the results.
Review for 10.1186/s12876-025-03912-0 (2025)

Title: Clinical characteristics of MASLD/MetALD/MAFLD/NAFLD and the relative risk
analysis on metabolic disorders
Version: 2 Date: 09 Apr 2025
Reviewer:  Giuseppe Guido Maria Scarlata
Reviewer's report:
In the present paper the Authors suggests that MAFLD is a more effective indicator for
identifying patients at increased risk for metabolic disorders. The paper il clear and well written.
However, i have some suggestions to improve it:
1. Underline the crucial role of the gut microbiota in the pathogenesis of fatty liver disease (see
10.20517/2394-5079.2023.134 );
2. Please, compare your study with other studies in the current literature. Moreover, consider
to address the key findings and the main criticisms of the different applications of these new
nomenclatures in the clinical context;
3. The methodological part was conducted with regards to ultrasound evaluation. However, the
transient elastography use deserves more attention;
4. I suggest to write an abbreviation list to facilitate the readers.
Review for 10.1186/s12876-025-03912-0 (2025)

Title: Clinical characteristics of MASLD/MetALD/MAFLD/NAFLD and the relative risk
analysis on metabolic disorders
Version: 2 Date: 12 Apr 2025
Reviewer's report:
This an interesting study comparing definitions of steatitic liver disease. It shows a peculiar
dysmetabolism segregation according to different definition of the syndrome.
It can have significant prognostic and preventive impact.
However, I have one criticism about the nature of the study: is it a retrospective ? on an existing
database ? This can bias the significance of results ? Please, discuss on this.
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 1 Date: 19 Feb 2025
Reviewer's report:
1. The first paragraph of the discussion section repeats content from the introduction and should
be deleted.
2. The paragraphs in the discussion section are excessively lengthy; it is advisable to break them
into shorter, more manageable segments for better clarity and understanding.
3. Although most of the included studies are observational, the article inaccurately categorizes
them as non-randomized clinical trials.
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 1 Date: 23 Feb 2025
Reviewer's report:
I have the following concerns about this manuscript and hope that the author to clarify.
1. The author needs to make adjustments to the format of this manuscript. When inserting a
(Figure), there should be a space. The same issue applies to, for example, the PRISMA flow
diagram. Could you please leave a blank line before each title?
2. It is not mentioned in the manuscript whether the clinical trial registration repositories
(ClinicalTrials.gov) or the grey literature have been searched. This may potentially lead to the
publication bias.
3. All the included studies are NRCTs, and no RCTs are included. Did the author attempt to
search for RCTs? If no RCTs were found, the author should discuss the impact of potential
biases of NRCTs on the results.
4. The NOS#7 points was used as the inclusion criterion, but the specific scoring details of each
study were not specified. The author is required to provide the detailed scoring results of each
study.
5. High heterogeneity was observed in some of the analyses. The author reduced the
heterogeneity by excluding some studies through sensitivity analysis. Are there any
methodological differences in these excluded studies? Can the potential sources of heterogeneity
be further explored?
6. For some analyses with relatively low heterogeneity (such as 1-year OS, the I² value was
not clearly reported), the author needs to clearly report all the heterogeneity in the results and
explicitly explain the applicability of the fixed-effect model.
7. The RR of 1-year OS is 0.38 (95% CI: 0.31–0.47), indicating a significant reduction in the
risk of death in the surgical group. However, is the HR more suitable for survival analysis? Has
the possibility of using HR instead of RR been considered to improve the clinical interpretability
of the results?
8. In the analysis of 3-year OS, the heterogeneity decreased after excluding the studies by Li
(2021) and Liang (2023). Could you provide a more detailed explanation of the reasons?
9. There was no significant difference in the CR rate, while the PR rate was significantly
increased. The author needs to explore the potential reasons for this contradictory result.
10. The author did not provide supplementary materials for the specific search strategy or
screening process. Will the complete search formula or the original screening records be
provided?
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 1 Date: 03 Mar 2025
Reviewer:  Muhammad Bakhtiar
Reviewer's report:
I have pointed out a few improvements to the best of my knowledge. The comments are meant
to make the the best possible final draft. Thank you.
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 3 Date: 23 Mar 2025
Reviewer's report:
Thanks for giving me the chance to review this manuscript. In this work, the authors aim
to compare the survival and toxicities outcomes Between Surgery and Non-Surgery After
Conversion Therapy for Advanced Gastric Cancer with Unresectable Factors. The authors
found that conversion surgerywas associated with improved 1-year, 3-year, and 5-year OS rates
(RR 0.38, 95% CI: 0.31–0.47; RR 0.64, 95% CI: 0.54–0.76; RR 0.77, 95% CI: 0.65–0.91,
respectively) and increased 1-year and 3-year PFS rates (RR 0.57, 95% CI: 0.49–0.99; RR 0.67,
95% CI: 0.57–0.78, respectively). However, one major limitation should be addressed.
There are inherent differences in prognosis between patients who undergo conversion surgery
and those who do not. Patients who response to conversion therapy typically proceed to surgery,
whereas those who fail to respond to conversion therapy and consequently cannot undergo
surgery tend to show poor therapeutic outcomes, resulting in poorer prognosis. Furthermore, the
studies included in the analysis are retrospective in nature, which makes selection bias in the
study population less controlled. Therefore, comparing therapeutic efficacy between these two
groups (responders vs. non-responders to conversion therapy) holds limited clinical significance.
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 3 Date: 27 Mar 2025
Reviewer's report:
The author has addressed all my concerns and I don't have further questions
Review for 10.1186/s12876-025-03969-x (2025)

Title: Comparison of Outcomes Between Surgery and Non-Surgery After Conversion Therapy
for Advanced Gastric Cancer with Unresectable Factors: A Systematic Review and Meta-
Analysis
Version: 4 Date: 18 Apr 2025
Reviewer's report:
The authors have responded adequately to the reviewer’s concerns. The manuscript now
appropriately contextualizes the findings and limitations, making it suitable for publication
in BMC Gastroenterology. No further revisions appear necessary regarding the selection bias
concern, though the editor may wish to consider whether the additional limitations identified in
this report warrant addressing before final acceptance.
Review for 10.1186/s12876-025-03974-0 (2025)

Title: The HbA1c/HDL-C Ratio as a Screening indicator of NAFLD in U.S. Adults:A Cross-
sectional NHANES Analysis (2017–2020)
Version: 1 Date: 31 Mar 2025
Reviewer's report:
Dear Editor,
Thank you for inviting me to review the manuscript entitled "Association Between the Plasma
Glycated Hemoglobin/High-Density Lipoprotein Cholesterol Ratio and NAFLD and Liver
Fibrosis Detected by Vibration-Controlled Transient Elastography in U.S. Adults: A Cross-
Sectional Analysis of NHANES 2017-2020."
This manuscript examines the association between the HbA1c/HDL-C ratio and the risk of
non-alcoholic fatty liver disease (NAFLD) and liver fibrosis in U.S. adults, utilizing data
from the 2017–2020 NHANES cohort. The authors used logistic regression, restricted cubic
splines (RCS), and receiver operating characteristic (ROC) analysis to evaluate the predictive
performance of HbA1c/HDL-C for NAFLD and liver fibrosis. Findings indicate a significant
positive correlation between HbA1c/HDL-C and NAFLD, while no significant association was
observed for liver fibrosis.
Clinical Comments
Clarify Clinical Implications for Non-Diabetic Populations
The study highlights that HbA1c/HDL-C predicts NAFLD better in non-diabetic individuals.
However, clinical implications for non-diabetic patients remain unclear. Are there specific
thresholds or population-based screening protocols that should be considered in this subset?
The authors should clarify how these findings could translate into personalized NAFLD risk
stratification.
Address Implications of Non-Significant Association with Liver Fibrosis
While the manuscript reports no significant association between HbA1c/HDL-C and liver
fibrosis, potential explanations (e.g., sample size, fibrosis stage variability, or lack of sensitivity
in elastography) should be provided to guide future research directions.
Statistical Comments
Consider Sensitivity Analyses for Threshold Effects
The RCS analysis identifies an inflection point at 5.743 for HbA1c/HDL-C and NAFLD.
However, sensitivity analyses exploring alternate inflection points or subgroup-specific
thresholds would enhance robustness and generalizability of this cut-off.
Provide Details on Model Calibration
While ROC and AUC values are reported, model calibration metrics such as Brier scores or
calibration plots should be presented to assess model accuracy. This ensures that predictions
remain accurate across different HbA1c/HDL-C ranges.
Review for 10.1186/s12876-025-03974-0 (2025)

Title: The HbA1c/HDL-C Ratio as a Screening indicator of NAFLD in U.S. Adults:A Cross-
sectional NHANES Analysis (2017–2020)
Version: 3 Date: 15 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The authors have provided comprehensive and thoughtful responses to all reviewer comments.
They have made appropriate revisions, acknowledged key limitations, and contextualized their
findings carefully. While the lack of a significant association between the HbA1c/HDL-C ratio
and liver fibrosis remains a limitation.
Review for 10.1186/s12876-025-03974-0 (2025)

Title: The HbA1c/HDL-C Ratio as a Screening indicator of NAFLD in U.S. Adults:A Cross-
sectional NHANES Analysis (2017–2020)
Version: 4 Date: 30 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
the responses are satisfactory
Review for 10.1186/s12876-025-03836-9 (2025)

Title: Investigation of the Mechanism by which miR-223-3p Inhibits Reflux Esophagitis
through Targeting the NLRP3 Inflammasome
Version: 3 Date: 30 Jan 2025
Reviewer:  Mohamed H. Zidan
Reviewer's report:
Dear Authors,
The study is well designed and the methodology is robust. However, the manuscript mentions
contradictory findings regarding miR-223-3p expression in reflux esophagitis (higher in some
studies, lower in others). This discrepancy should be discussed in greater depth, possibly
exploring factors such as disease stage, tissue specificity, or methodological differences that
could explain the variation. Second, while the study demonstrates that miR-223-3p targets
NLRP3, the precise molecular mechanisms by which miR-223-3p regulates NLRP3 activation
(e.g., through NF-#B or other pathways) remain unclear. A more detailed discussion of potential
signaling pathways would strengthen the mechanistic insights.
Review for 10.1186/s12876-025-03836-9 (2025)

Title: Investigation of the Mechanism by which miR-223-3p Inhibits Reflux Esophagitis
through Targeting the NLRP3 Inflammasome
Version: 3 Date: 14 Feb 2025
Reviewer's report:
The manuscript by Shuying Lin et al. describes the protective role of miR-223-3p against reflux
esophagitis. Overexpression of miR-223-3p markedly inhibited NLRP3 expression, reduced the
release of inflammatory factors, decreased cell apoptosis, promoted cell cycle progression, and
enhanced cell viability. However, their conclusions are based solely on experiments conducted
using a single cell line (HET-1A). While the regulatory mechanisms of miR-223-3p play a key
role in reducing inflammation and cellular damage in reflux esophagitis by targeting the NLRP3
inflammasome, these mechanisms need to be further explored. I recommend that the authors
include experiments utilizing mouse models or human samples that focus on reflux esophagitis.
Review for 10.1186/s12876-025-03836-9 (2025)

Title: Investigation of the Mechanism by which miR-223-3p Inhibits Reflux Esophagitis
through Targeting the NLRP3 Inflammasome
Version: 4 Date: 18 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03836-9 (2025)

Title: Investigation of the Mechanism by which miR-223-3p Inhibits Reflux Esophagitis
through Targeting the NLRP3 Inflammasome
Version: 4 Date: 29 Mar 2025
Reviewer:  Mohamed H. Zidan
Reviewer's report:
Dear Authors,
All the changes are satisfactory. Thank you for your revisions and comments
Review for 10.1186/s12876-025-03966-0 (2025)

Title: Nonlinear Association between AST/ALT Ratio and 28-Day All-Cause Mortality
Following ICU Admission in Critically Ill Cirrhotic Patients: A Retrospective Cohort Study
Version: 1 Date: 31 Mar 2025
Reviewer's report:
The authors should include either a supplemental page describing the ICD codes used to identify
the "cirrhotic" patient population or describe a significant limitation of the study in using ICD
codes to accurately identify the population of interest.
It would be helpful to describe other biomarkers which could suggest AST elevation not due
to  liver injury for example CK or troponin as this would have significant implications for the
interpretation of this data.
Review for 10.1186/s12876-025-03966-0 (2025)

Title: Nonlinear Association between AST/ALT Ratio and 28-Day All-Cause Mortality
Following ICU Admission in Critically Ill Cirrhotic Patients: A Retrospective Cohort Study
Version: 3 Date: 30 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
the responses are satisfactory
Review for 10.1186/s12876-025-03966-0 (2025)

Title: Nonlinear Association between AST/ALT Ratio and 28-Day All-Cause Mortality
Following ICU Admission in Critically Ill Cirrhotic Patients: A Retrospective Cohort Study
Version: 3 Date: 01 May 2025
Reviewer's report:
i have no further comments
Review for 10.1186/s12876-025-03975-z (2025)

Title: Red cell distribution width as a potential new biomarker to predict the clinical severity
of acute diverticulitis
Version: 1 Date: 06 Mar 2025
Reviewer's report:
Thank you for allowing me to review the manuscript from Melek Yalcin Koc et al, entitled
“Red cell distribution width as a potential new biomarker to predict the clinical severity of acute
diverticulitis”.
Congratulation to the authors for their remarkable work. In my opinion, the subject is of interest
but the manuscript in this present form is too long and too difficult to read. It should be shorten
and the results should focus on the objective (compare the diverticultis).
Abstract : OK
Introduction: ok
MM: were all the acute diverticulitis confirmed by colonoscopy? This is surprising because the
colonoscopy in this context is at risk for perforation. Is this a routine examination in you hospital?
How was chosen the control group? Who are the patients ?
Why did the authors choose to include a control group? The objective is to investigate the
relationship between RDW other inflammatory markers and some clinical features with the
presence, and clinical and radiological severity of acute diverticulitis. I am not sure that this is
necessary (the control group should be the patient that have no severe diverticulitis)
Results:
The first part of the results does not add something to the literature (older age, WBC and CRP
are associated with the risk of diverticulitis)
I would suggest to reduce the result section and limit to the comparisons of severe diverticulitis
and the need for surgery.
The need for surgery should be defined (immediate surgery or failure of conservative
management)
I would be interested in having the results of creatininemia (influence of renal failure on RDW)
Discussion
Should be shorten and focused on the results.
Please explain why the RDW would be increased in patients with diverticulitis requiring
surgery? What should be the pathophysiology?
Review for 10.1186/s12876-025-03975-z (2025)

Title: Red cell distribution width as a potential new biomarker to predict the clinical severity
of acute diverticulitis
Version: 2 Date: 06 Apr 2025
Reviewer's report:
I am satisfied that the authors have adequately addressed comments made in the first round of
reviews, and would be happy to support this article for publication.
Review for 10.1186/s12876-025-03828-9 (2025)

Title: Factors predicting conversion from Colon Capsule Endoscopy to Conventional Optical
Endoscopy - findings from the CESCAIL Study
Version: 4 Date: 18 Feb 2025
Reviewer:  Konosuke Nakaji
Reviewer's report:
Colon capsule endoscopy (CCE) is considered a non-invasive, safe, and environmentally
friendly (low CO2 emission) screening method for colorectal cancer compared to other
modalities. However, contrary to initial expectations, its global adoption has not progressed
as anticipated. This study examines factors leading to conversion to conventional colonoscopy
(CCC) due to incomplete CCE, using data from an existing study (CESCAIL study: comparison
of polyp detection rates in CCE between humans and AI). Although it has limitations as a
retrospective analysis of existing data, this research is considered highly valuable for improving
the acceptability and cost-effectiveness of CCE, which has drawbacks of laxative-related
discomfort and high cost, and for reducing CCC conversions to promote CCE adoption.
The study found that non-smokers with low f-Hb levels are less likely to require conversion to
conventional endoscopy (CCC). Furthermore, it showed that being a male, non-diabetic, non-
smoker, and non-alcoholic consumer reduces the risk of incomplete capsule excretion. Overall,
there are no significant issues, but there are some points of concern:
1. For readers unfamiliar with CCE, please describe the features of second-generation CCE (e.g.,
AFR function) and its accuracy (sensitivity and specificity compared to CS as the gold standard).
Was there a standardized laxative regimen? How was the image interpretation conducted
(including human and AI methods)? What is the price of CCE compared to conventional CS?
2. Does "smoker" include past smoking? What is the quantity of alcohol consumed by alcohol
consumers? What are the definitions of hyperlipidemia and psychological state scales? Should
the education level of subjects have been considered? Is the definition of IBD appropriate for
UC and CD? Does diabetes include only Type 2?
3. What specific size (in millimeters) is considered "large" for polyps? Was the Paris
classification used for polyp morphology?
4. The text states, "Inappropriate CCE is assumed to have been converted mainly to conventional
CS rather than repeating CCE or proceeding to CT colonography. This is mainly due to concerns
about inadequate bowel preparation." Did these patients have prior experience with conventional
endoscopy before undergoing CCE?
Review for 10.1186/s12876-025-03828-9 (2025)

Title: Factors predicting conversion from Colon Capsule Endoscopy to Conventional Optical
Endoscopy - findings from the CESCAIL Study
Version: 4 Date: 26 Feb 2025
Reviewer:  Sergio Coda
Reviewer's report:
The manuscript is very well written, a pleasure to read and results are accurately and correctly
reported. There is value in highlighting predicting factors  associated with CCE and the study
successfully analyses those. I am certain all CCE readers/users will be pleased to read it.
Review for 10.1186/s12876-025-03828-9 (2025)

Title: Factors predicting conversion from Colon Capsule Endoscopy to Conventional Optical
Endoscopy - findings from the CESCAIL Study
Version: 5 Date: 24 Mar 2025
Reviewer:  Konosuke Nakaji
Reviewer's report:
The authors have revised their article according to the reviewer's comments, improving the
article. No further comments are available.
Review for 10.1186/s12876-025-03828-9 (2025)

Title: Factors predicting conversion from Colon Capsule Endoscopy to Conventional Optical
Endoscopy - findings from the CESCAIL Study
Version: 5 Date: 24 Mar 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-03955-3 (2025)

Title: Association of Biological Aging and the Prevalence of Nonalcoholic Fatty Liver Disease:
a Population-based Study
Version: 0 Date: 18 Feb 2025
Reviewer's report:
The authors have evaluated the association of biological aging markers with NAFLD.
(1) The definition of NAFLD is based on exclusion criteria, those with underlying liver diseases
or significant alcohol intake should be excluded. What the authors have defined is hepatic
steatosis or steatotic liver disease.
(2) The approach is interesting, but it is not surprising  that biological aging markers are
associated with steatotic liver disease. If the authors have done Z-score normalization for 4
markers (AL, HD, KDM, phenoage), rank them, and discuss which one is most effective and
why, then this study would have significant novelty.
Review for 10.1186/s12876-025-03955-3 (2025)

Title: Association of Biological Aging and the Prevalence of Nonalcoholic Fatty Liver Disease:
a Population-based Study
Version: 0 Date: 28 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-A brief explanation of each biological aging metric (KDM-BA, PA, HD, AL) and how they
were calculated would be helpful for readers who are not familiar with these terms.
-It would be useful to elaborate on how missing data were handled in the analysis and if any
imputation or exclusion strategies were used.
-It would be helpful to briefly mention the advantages and limitations of using FLI # 60 as a
diagnostic criterion for NAFLD, especially in a diverse population.
While subgroup analyses are mentioned, more details about the specific subgroups analyzed
(e.g., by age, gender, race/ethnicity) would enhance clarity.
-While the discussion mentions epigenetic factors like DNA methylation and chromatin
remodeling, it could be enhanced by a more specific discussion of how these mechanisms
might directly influence NAFLD or its progression. For example, how could DNA methylation
patterns in liver tissue contribute to NAFLD? This connection would help bridge the findings
of biological aging with the specific pathology of NAFLD.
-While the discussion highlights NAFLD and its relation to biological aging, there could be more
exploration of how other coexisting conditions, such as diabetes, hypertension, or cardiovascular
disease, might further exacerbate the relationship between aging and NAFLD. -This might
provide a more holistic view of the health risks.
While the limitations of the study are acknowledged (cross-sectional design and sample size),
it could be helpful to expand on how these limitations might affect the interpretation of the
findings. For instance, while causality cannot be established, are there other ways in which the
results can still inform future longitudinal studies or clinical trials?
-While epigenetic aging is mentioned as the most accurate method of assessing biological age,
a little more explanation could be helpful for readers who may not be familiar with epigenetic
clocks. For example, how do these clocks work in practice, and what makes them more reliable
than other biomarkers?
-The conclusion could briefly mention the potential clinical or public health implications of these
findings. For example, would early interventions targeting biological aging metrics be beneficial
in preventing or managing NAFLD? Offering a hint at future directions or practical applications
would increase the impact of the conclusion.
Review for 10.1186/s12876-025-03955-3 (2025)

Title: Association of Biological Aging and the Prevalence of Nonalcoholic Fatty Liver Disease:
a Population-based Study
Version: 1 Date: 30 Mar 2025
Reviewer's report:
Liu et al. found an independent association between the aging biomarkers with NAFLD in the
NHANES database. This study is clear and technically sounds. However, the association of
aging with NAFLD is already known, but yet not comprehensively understood finding. I only
have a few concerns:
1. Current understanding on aging and NAFLD needs to be introduced. For example, the
prevalence of NAFLD was 44.2% (269441/608994) for older adults in South Korea (Clin
Mol Hepatol. 2022;28(3):510-521). The prevalence of NAFLD in all age groups (20-39 young
adults, 40 or above, >=65 older adults) need to be introduced to better deliver currently known
knowledge.
2. 2.4 Calculation of Biological Aging is too simple. Can you provide a brief description on how
did you evaluate the biomarkers?
3. There is no direct discussion why aging may lead to the liver fat accumulation. It may be due
to accumulation of fat within the liver or weakened ability to clear fat contents within the liver.
Review for 10.1186/s12876-025-03880-5 (2025)

Title: Efficient diagnosis for endoscopic remission in Crohn’s diseases by the combination of
three non-invasive markers
Version: 2 Date: 25 Dec 2024
Reviewer's report:
The study presents a novel approach to diagnosing endoscopic remission (ER) in Crohn's disease
(CD) by combining three non-invasive markers: serum C-reactive protein (CRP), leucine-rich
alpha-2 glycoprotein (LRG), and fecal calprotectin (Fcal). The authors aimed to enhance the
diagnostic performance of ER by evaluating the efficacy of these markers in combination, rather
than in isolation, which has been the norm in previous studies.
I have some comments/concerns to be addressed:
1.The study's innovation is marginal, as it follows the established trend of multi-biomarker
assessments in IBD without introducing a transformative approach.Furthermore, it does not
compare the efficacy of the chosen biomarker panel with other panels proposed in similar past
studies, which limits the assessment of its relative performance and potential superiority.
2.The question at hand is why these 3 biomarkers were chosen when there are numerous other
non-invasive biomarkers available as candidates.
3.It is necessary to clarify the cut-off values and detection limits for LRG, CRP, and Fcal.
Concurrently, a test for normal distribution of the quantitative data must be conducted.
Review for 10.1186/s12876-025-03880-5 (2025)

Title: Efficient diagnosis for endoscopic remission in Crohn’s diseases by the combination of
three non-invasive markers
Version: 2 Date: 31 Dec 2024
Reviewer's report:
Endoscopic assessments are inconvenient for many IBD patients. Therefore, this manuscript,
which investigates the value of non-invasive biomarkers for detecting endoscopic remission, is
highly relevant to the field.
I have the following remarks for the authors:
1- The manuscript frequently uses the term “predict.” However, “predict” implies that biomarker
values are measured at a time point preceding the endoscopic assessments. Since the biomarkers
in this study are measured simultaneously with the endoscopic assessments, it would be more
appropriate to use the term “monitor”.
2- What statistical tests were used to compare AUC, sensitivity, and other metrics between single
biomarkers, combinations of biomarkers, or the two-step approach?
3- It is unclear why the authors chose to use Support Vector Machines or which variables were
included as inputs in this machine learning process. Additionally, the manuscript refers to K-
fold cross-validation as a “machine learning” method, but it is actually a “resampling” method.
- To address points 2 and 3, the authors could select an appropriate statistical test to
compare p-values. Furthermore, robust resampling methods, such as K-fold cross-validation or
bootstrapping, should be employed to estimate uncertainty in confidence intervals.
4- Were CDAI values available at all endoscopic time points?
Since the study aims to investigate the role of “non-invasive” tools in monitoring endoscopic
disease activity, I recommend including clinical disease activity measures in the comparison.
Assessing clinical symptoms is even easier than obtaining the three biomarkers evaluated in this
study and could provide additional context.