JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-04137-x (2025)

Title: Unraveling the link between Inflammatory Bowel Disease and Perianal Abscess: Insights
from Bidirectional and Multivariable Mendelian Randomization Study
Version: 2 Date: 10 Mar 2025
Reviewer's report:
This study explores the causal relationship between inflammatory bowel disease and perianal
abscess using Mendelian Randomization. Several methodological and interpretational concerns
need to be addressed to strengthen the manuscript’s validity.
Major
1. The authors did not discuss potential weak instrument bias . Besides, consider adding MR-
Steiger filtering to confirm the direction of causality.
2. The de Lange et al. dataset includes a subset of participants from the International IBD
Genetics Consortium , leading to potential sample overlap between the discovery and replication
cohorts. A truly independent is needed for replication.
3. The MVMR model adjusts for BMI, smoking, and diabetes, but no justification is given for
selecting these confounders.
4. Bonferroni correction is recommended for multiple testing, particularly in exploratory
subgroup analyses (e.g., ulcerative ileocolitis and PA).
5. The clinical relevance of findings could be better articulate
Minor
1. some typo in the manuscript. Like “a chronic chronic inflammatory condition that varies in
severity”
Review for 10.1186/s12876-025-04137-x (2025)

Title: Unraveling the link between Inflammatory Bowel Disease and Perianal Abscess: Insights
from Bidirectional and Multivariable Mendelian Randomization Study
Version: 4 Date: 27 Jun 2025
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: The revised manuscript significantly enhances scientific rigor and
clarity. Key methodological improvements include the incorporation of MR-Steiger filtering,
expanded sensitivity analyses, and thorough adjustment for confounders in multivariable
MR. The authors appropriately acknowledge the limited power in reverse MR due to sparse
instruments and distinguish exploratory subgroup findings. Clinical implications are now more
precisely articulated and grounded in current evidence. Overall, the revision addresses prior
concerns effectively, enhances reproducibility, and reinforces the validity of the findings.
ADDITIONAL REQUESTS/SUGGESTIONS:
The text remains somewhat dense and technical in places (e.g., “pleiotropy-robust analytical
approaches”), and a round of native English editing was recommended. The manuscript is
scientifically sound and appears suitable for acceptance, pending final language polishing to
enhance clarity.
Review for 10.1186/s12876-025-04141-1 (2025)

Title: Correlation between systemic inflammatory response syndrome and prognosis of patients
with cirrhosis and hepatic encephalopathy
Version: 2 Date: 05 May 2025
Reviewer's report:
Recent studies have revealed important findings regarding cirrhotic patients, indicating that
the presence of Systemic Inflammatory Response Syndrome (SIRS) significantly affects their
survival rates. This discovery is fascinating and highlights the importance of a well-structured
work schedule.
Review for 10.1186/s12876-025-04141-1 (2025)

Title: Correlation between systemic inflammatory response syndrome and prognosis of patients
with cirrhosis and hepatic encephalopathy
Version: 2 Date: 06 May 2025
Reviewer:  Iliana Mani
Reviewer's report:
Dear Editor
This is an interesting study, examining prevalence and significance of SIRS in cirrhotic patients
with encephalopathy. Although of clinical interest, this study faces some limitations. My main
concern is the methods applied for selection of patients.
Major comments
• Methods: More details are needed for the exclusion criterion “patients who were diagnosed
with serious primary conditions of other major systems” as it is too general.
• Patients management: This section describes a specific and homogenous method of identifying
and treating patients with HE. For example: “All patients were examined within 24 hours of
admission”, “If infection was suspected, samples for blood, urine and sputum cultures were
promptly collected”. However, as authors stated, the study is retrospective. How did authors
identify such information? Please clarify.
• Multivariate analysis: Although sodium was not of clinical significance in univariate analysis,
authors included it in multivariate analysis. Please explain or change accordingly.
Minor comments
• Abstract: In results, authors should provide information about total number of patients, their
demographic characteristics and markers of severity of liver disease such as MELD or Child
Pugh score.
• Introduction: Please rephrase
- “acute portal hypertension”
- "Among patients suffering decompensated cirrhosis, hepatic encephalopathy (HE) manifesting
with neuropsychiatric abnormalities is the most frequent complication" Please rephrase as HE
is not more common than ascites or variceal bleeding [D'Amico G et al. J Hepatol 2022
Jan;76(1):202-207]. Moreover, the provided references do not support such statement.
• Risk factors of death during hospitalization:  “Univariate and multivariate Cox”. Please
rephrase as multivariate analysis is mentioned separately.
• Please use were instead of was in “Correlations among significant variables was..."
Review for 10.1186/s12876-025-04167-5 (2025)

Title: Association of Red Blood Cell Distribution Width with Short- and Long-Term All-Cause
Mortality in Patients with Acute Pancreatitis and Sepsis
Version: 2 Date: 29 Apr 2025
Reviewer's report:
1. The criteria for exclusion are too vague and should theoretically exclude patients with other
blood disorders as well as pregnant women and cancer patients.
2. data with missing values greater than 15% should be excluded, and those that are indeed less
than 15% should be interpolated using multiple interpolation.
3. what is the basis for the grouping of RDW?
4. The results section is too simple and lacks in-depth interpretation.
5. The citations of RDW related articles are not comprehensive.
Review for 10.1186/s12876-025-04167-5 (2025)

Title: Association of Red Blood Cell Distribution Width with Short- and Long-Term All-Cause
Mortality in Patients with Acute Pancreatitis and Sepsis
Version: 2 Date: 17 May 2025
Reviewer's report:
This study, through statistical analysis of patients with AP complicated by sepsis in the MIMIC-
IV database, revealed the potential value of RDW in the prognosis assessment of AP patients
with sepsis, providing a simple and low-cost predictive tool for clinical practice. It has significant
clinical value. I have several questions and hope to receive the author's answers:
1. For AP patients complicated by sepsis, is the source of infection secondary infection of
pancreatic necrotic tissue or infection of other organs outside the pancreas?
2. What is the statistical basis for grouping using the median RDW value?
3. It is well known that AP patients complicated by sepsis have already developed severe
complications such as IPN or organ failure. Can the proportion of patients with severe AP and
the number of surgical interventions in the two groups after grouping be described?
4. The author only used the first RDW test value after admission and did not analyze the
relationship between its dynamic changes and prognosis, such as the trend of RDW changes at
28 days, 90 days, and 365 days.
Review for 10.1186/s12876-025-04167-5 (2025)

Title: Association of Red Blood Cell Distribution Width with Short- and Long-Term All-Cause
Mortality in Patients with Acute Pancreatitis and Sepsis
Version: 2 Date: 02 Jun 2025
Reviewer's report:
I Thank the editor and authors for inviting me to review the manuscript titled “Association of Red
Blood Cell Distribution Width with Short- and Long-Term All-Cause Mortality in Patients with
Acute Pancreatitis and Sepsis: A Retrospective Analysis based on the MIMIC-IV database”.
The manuscript presents a well-defined research question and provides a comprehensive review
of the relevant literature. However, there are several issues that need to be addressed before the
manuscript can be published.
Abstract
1. It is recommended to include the HR (Hazard Ratio) and confidence interval for the results.
Introduction
1. we addressed the prognostic value of RDW by examining its impact on patients with AP and
sepsis.-> It is recommended to change impact to association.
Materials and methods
1. Have diseases that affect RDW, such as anemia, been excluded?
Results
3.3 Cox regression models
1. It is recommended to include the HR (Hazard Ratio) and confidence interval for the different
endpoints.
2. What are the criteria for covariate adjustment? Is there a risk of over adjustment?
Review for 10.1186/s12876-025-04167-5 (2025)

Title: Association of Red Blood Cell Distribution Width with Short- and Long-Term All-Cause
Mortality in Patients with Acute Pancreatitis and Sepsis
Version: 4 Date: 06 Jul 2025
Reviewer's report:
Thank you for the author's reply. It is suggested that the Cox regression results (HR and
95%CI)for 90 days and 365 days mortality also be included in the Results section.
Review for 10.1186/s12876-025-04167-5 (2025)

Title: Association of Red Blood Cell Distribution Width with Short- and Long-Term All-Cause
Mortality in Patients with Acute Pancreatitis and Sepsis
Version: 7 Date: 14 Jul 2025
Reviewer's report:
The authors have addressed the issues I raised, and I agree to accept the manuscript.
Review for 10.1186/s12876-025-04122-4 (2025)

Title: Analysis of influencing factors and nursing strategies for enteral nutrition patients
complicated with refeeding syndrome in ICU
Version: 1 Date: 12 Feb 2025
Reviewer's report:
The article is based on a retrospective analysis of 173 patients admitted to the ICU in 2020-2021.
The division into the control and observational group is well justified, and the inclusion and
exclusion criteria are clearly defined. The study employs statistical analysis using the t-test,
chi-square test, and multivariate logistic regression, which allows for inferences about the
relationships between risk factors and refeeding syndrome (RS). However, the lack of long-term
patient follow-up and the limited number of participants may affect the generalizability of the
results.
The study results indicate that the key risk factors for RS include: age # 60 years, high NRS
2002 score, long mechanical ventilation time (# 3 days), high APACHE II score, rapid feeding
rate (>50 ml/h), protein intake # 1.2 g/kg, and enteral feeding temperature. It has been shown
that the use of targeted nursing strategies contributes to the improvement of electrolyte levels
(phosphorus, potassium, magnesium), albumin, and prealbumin in patients with RS, confirming
the effectiveness of the intervention.
The conclusions of the article are consistent with the study results. The importance of early
identification of risk factors and the implementation of individualized nursing strategies to
reduce the incidence of RS is emphasized.
The discussion in the article addresses the most important aspects of the results. The authors
compare their findings with other studies, emphasizing the importance of monitoring patients
for RS and the significance of targeted nursing interventions. However, it could be more detailed
in terms of clinical implications and possible methodological limitations of the study, such as
the influence of other independent variables that may have affected the outcome.
The study has some limitations, including the lack of long-term patient follow-up and the
absence of an analysis of the influence of other potential factors (e.g., type of comorbidities).
The article is a valuable contribution to the topic of refeeding syndrome in ICU patients. The
results provide important information on risk factors and the effectiveness of nursing strategies.
The study's limitations indicate the need for further research in this area.
Review for 10.1186/s12876-025-04122-4 (2025)

Title: Analysis of influencing factors and nursing strategies for enteral nutrition patients
complicated with refeeding syndrome in ICU
Version: 1 Date: 14 Feb 2025
Reviewer's report:
The article “Analysis of influencing factors and nursing strategies in patients with enteral
nutrition complicated by re-feeding syndrome in the ICU” presents the surprising conclusion
that refeeding syndrome (RF) was common in the ICU in critically ill patients fed with enteral
nutrition.
However, most studies have shown that:
RF is usually associated with pure anabolism and deficit in intracellular mineral uptake, which
is a rare situation in ICU patients
RF is less common in patients on enteral nutrition, because it is very difficult to achieve a positive
result with enteral nutrition alone in ICU conditions.
However, the article has many pitfalls.
This is a retrospective work.
The diagnostic criteria for RF are not characterized.
The amount and form of energy (carbohydrates and lipids) and minerals during enteral nutrition
are not described.
Was the composition of the enteral nutrition the same in the patients?
In its current form, the article cannot be published because the results are not sufficiently
documented, which may lead to their misinterpretation.
Review for 10.1186/s12876-025-04049-w (2025)

Title: LINC00634 is a novel prognostic biomarker for colon cancer associated with immune
infiltration
Version: 2 Date: 30 Dec 2023
Reviewer:  Giovanni Tomasicchio
Reviewer's report:
In this interesting study, the author used bioinformatics methods to screen genes related to
colon cancer, by constructing a predictive model, conducting in vitro experiments, and analyzing
its relationship with TIME. They showed a novel prognostic biomarker for colon cancer,
LINC00634. However, the author needs to improve the methods and results sections of the
paper. I suggest the authors follow the STROBE guidelines before writing a paper.
I have several questions for the author:
- In your introduction, you explain the role of TIME and lncRNAs in the progression of cancers,
but you didn’t explain their relationship. This is a key point for the aim of your study that you
wrote only at the end of the discussion. Please add, with references, in your introduction.
- Material and Methods is a crucial part of the paper, to understand results and discussion. You
need to modify your material and methods: you divided it in different paragraphs, writing parts
of the methods in the results, omitting information, and becoming unclear to the reader.
For example, you made a Kaplan-Meier analysis but didn’t write it in methods but directly in
results. Please write a single paragraph following the STROBE statement.
- Split the methods from the statistical part, you don’t need to write it for the different variables.
- Please add your study design in material and methods, you didn’t write it clearly in the text.
- Also, in the Results section, you made a mix of methods and discussion. You need to write only
your result you should not suggest your idea or discuss it in results. For example: “suggesting
that this gene set has potential ability to predict the prognosis of patients with colon cancer” or
“These results suggest that LINC00634” or “mediates the alteration of the immune environment
in colon cancer aroused our curiosity”
Review for 10.1186/s12876-025-04049-w (2025)

Title: LINC00634 is a novel prognostic biomarker for colon cancer associated with immune
infiltration
Version: 4 Date: 13 Aug 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: The authors have responded to my comments and incorporated
changes into the paper. If the additional tables are too long to be published then the tables can
be included as supplementary material. The paper has been improved and it will be easier for
others to reproduce the findings.
ADDITIONAL REQUESTS/SUGGESTIONS:
I have no further comments.
Review for 10.1186/s12876-025-04125-1 (2025)

Title: Efficacy and safety of vedolizumab in elderly and younger patients with moderate-to-
severe ulcerative colitis: A retrospective real-world study in China
Version: 1 Date: 09 Apr 2025
Reviewer's report:
Dear Zhang et al.,
Thank you for this interesting and overall well-written manuscript. Although no evaluation has
been done specifically in Chinese elderly patients, efficacy and safety have been studied in
elderly populations in general. Nonetheless, the study remains relevant given the size of the
Chinese population. Below are my comments:
1. The study carries a selection bias, as physicians generally tend to avoid prescribing VDZ to
non–bio-naive patients from the outset.
2. The manuscript does not explain why only patients who had received three infusions prior to
inclusion were selected. Several other studies include patients starting from the first infusion.
3. The data collection method is not described. Was data manually extracted from patient charts?
4.It is not stated whether a univariable or multivariable regression model was used, nor how the
model was selected.
5. Information is missing on the completeness of data at each timepoint, which is particularly
relevant given the high standard deviations reported at each visit.
6. A discussion is lacking on why the follow-up duration was significantly shorter in elderly
patients compared to younger ones.
7. The authors state that concomitant corticosteroid use was associated with an increased risk of
adverse events. However, the reported OR was 0.05, which would normally indicate a protective
effect. How was this analysis performed?
8. It is stated that hemoglobin increased markedly, but the change was from 7.0 mmol/L to 7.2
mmol/L. While this may be statistically significant, is it clinically relevant?
9. I suggest that the authors perform a Cox regression analysis, given that a Kaplan-Meier plot
was presented.
Minor comments:
Some terminology used is not standard in IBD research. For example, "total colitis" is
more commonly referred to as "extensive colitis" or "pancolitis." The term "comprehensive
assessment by the physician" is unclear—does this refer to a global assessment?
Consider rephrasing the sentence on line 233.
On line 285, it is stated that only one patient had a lung infection, while line 294 states two
patients. Please clarify.
I was unable to open any of the TIFF files, despite trying several programs and converting them
to PNG.
Review for 10.1186/s12876-025-03988-8 (2025)

Title: Global Burden of Esophageal Diseases: A Comprehensive Analysis of Disease Trends
and Risk Factors from 1990 to 2021
Version: 2 Date: 17 Apr 2025
Reviewer's report:
The author has gone to considerable effort to elaborate on this theme, but I have several major
considerations
1. As a member of the GBD collaboration, I remember that GBD2023 data is coming out, and
this study doesn't make much sense.
2. This topic you have done is not novel. Many articles have elaborated on this topic. I don't
see any relevant innovation points.
3. The discussion is not rich in content and appears to be very vague.
Therefore, I strongly refuse to publish this article
Review for 10.1186/s12876-025-03988-8 (2025)

Title: Global Burden of Esophageal Diseases: A Comprehensive Analysis of Disease Trends
and Risk Factors from 1990 to 2021
Version: 2 Date: 22 Apr 2025
Reviewer:  Haoyu An
Reviewer's report:
Overall Recommendation:
Minor Revision
This manuscript provides new insights into the evolving epidemiology of esophageal disorders.
The authors should address the reviewers' technical comments to strengthen the manuscript's
scientific rigor.
1. The description of esophageal diseases (ED) as 'mainly including gastroesophageal
reflux disease (GERD) and esophageal cancer (EC)' requires refinement. Current clinical
classifications typically encompass a broader spectrum, including GERD, esophagitis, Barrett's
esophagus, achalasia, and esophageal cancer.
2. The statement regarding the high recurrence rate of GERD and poor prognosis of EC
contributing to disease burden would benefit from appropriately cited references.
3. While the application of Bayesian age-period-cohort (BAPC) modeling is appropriate, the
methodological description requires expansion to ensure reproducibility. Perhaps you can refer
to this article (10.1007/s10620-024-08465-y).
4. The current analysis of population attributable fractions (PAF) focuses exclusively on EC
risk factors. To enhance the study's comprehensiveness, supplementing the analysis of GERD-
related risk factors for its burden indicators would provide more valuable insights.
5. The isolated presentation of analysis software and statistical thresholds in separate sections
may affect methodological clarity. I recommend consolidating all technical specifications
(including software versions and significance thresholds) within the Methods section for
improved readability.
6. The identification of key risk factors in Figure 9 would benefit from clearer methodological
justification. Prior to conducting population attributable fraction (PAF) analysis, it is essential
to establish an evidence-based selection process for included risk factors. I recommend
either a) explicitly referencing established risk factor hierarchies from authoritative sources
or b) conducting a systematic literature review to justify factor inclusion using predefined
selection criteria. This methodological transparency is critical for validating the 'key risk factor'
designation.
Review for 10.1186/s12876-025-03988-8 (2025)

Title: Global Burden of Esophageal Diseases: A Comprehensive Analysis of Disease Trends
and Risk Factors from 1990 to 2021
Version: 2 Date: 26 Apr 2025
Reviewer:  Amal Arifi Hidayat
Reviewer's report:
The authors investigated the global distribution of ED and conducted a thorough temporal
analysis. The methodology is robust, and the discussion is insightful, offering valuable
perspectives. Only a few minor revisions are needed to further enhance the overall quality and
readability of the paper.
Minor Revisions:
1. In line 368-369, the authors stated that low and low-middle SDI regions should prioritize
GERD management and EC nutritional interventions. A more detailed review of nutritional
interventions related to EC is suggested to enhance the cohesiveness of the discussion.
Review for 10.1186/s12876-025-04107-3 (2025)

Title: Development and Validation of Predictive Models for Disease-free Survival and
Overall Survival in Non-metastatic Right-Sided Colon Adenocarcinoma Patients Based on
Inflammatory and Nutritional Indices
Version: 4 Date: 20 Jun 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
The responses are satisfactory
Review for 10.1186/s12876-025-04108-2 (2025)

Title: The effect of neoadjuvant chemoradiation therapy in resectable pancreatic cancer was
independent of intratumoral vascularization
Version: 2 Date: 07 Feb 2025
Reviewer's report:
Thank you for giving me the opportunity to review this paper. The manuscript entitled " The
effect of neoadjuvant chemoradiation therapy in resectable pancreatic cancer was independent
of intratumoral vascularization" mainly revealed that the histopathological efficacy of NACRT
for resectable PC did not differ significantly on the basis of enhancement pattern observed on
CH-EUS.
This is an interesting study and has certain clinical significance. My comments and questions
are as follows.
1, In the definition of resectable PC, it says “3) Tumors that have achieved downstaging from T4
to the above criteria after neoadjuvant chemotherapy” I don't think T4 is classified as resectable
PC. If you are including T4 cases, you should change the title and method.
2, A small number should be given as a limitation.
3, At the end of the discussion, the authors state that “our study affirms the efficacy of NACRT
in enhancing therapeutic outcomes,,,” but the main point of this study is that NACRT seems
to reduce the variations in chemotherapeutic efficacy caused by fibrosis-induced blood flow
disparities. Since this is not a study that proves the efficacy of NACRT, I think it would be better
to change the wording.
Review for 10.1186/s12876-025-04108-2 (2025)

Title: The effect of neoadjuvant chemoradiation therapy in resectable pancreatic cancer was
independent of intratumoral vascularization
Version: 2 Date: 26 Feb 2025
Reviewer's report:
Thank you for giving me the invaluable opportunity to review this manuscript. The authors
reported a retrospective study assessing the effect of neoadjuvant chemoradiation therapy in
resectable pancreatic cancer and its relationship with Intratumoral vascularity by contrast-
enhanced harmonic EUS.
The authors still need the following major revisions:
1. (Page 12-13 Line 49-55)
Resectable PC was defined as follows: 1) a tumor without extension into the superior mesenteric
artery, celiac artery or common hepatic artery; 2) a tumor with an abutment/encasement or a
short segment of occlusion into the superior mesenteric vein (SMV) and portal vein (PV); or 3) a
tumor that achieved downstaging after neoadjuvant chemotherapy from T4 to the above criteria.
We need more explanation on the definition of resectable pancreatic cancer, why the criteria
in this paper were different from resectability status in NCCN guideline? criterion 2) should
be considered as borderline resectable, and criterion 3) the inclusion of induced resectable
pancreatic cancer could be misleading, the authors need to clarify the rationale.
2. (Page 16-17 Line 89-94)
All patients were treated preoperatively with chemoradiation therapy. For systemic
chemotherapy, gemcitabine (1000 mg/m2) monotherapy was administered to 41 patients on days
1, 8, and 15 of each 28-day cycle. S-1 (120 mg/d) monotherapy was administered to 5 patients
for 4 weeks at 2-week intervals. Two patients were administered a combination of gemcitabine
(1000 mg/m2) and nab-PTX (125 mg/m2). Three-dimensional radiation was delivered at a total
radiation dose of 50 Gy in daily fractions of 2 Gy, 5 times per week.
The authors need to provide more specific details on chemoradiation therapy. How many cycles
of chemotherapy? What duration of radiotherapy did these patients receive before the surgical
resection?
3. Page 23 Line 157 and Page 25 Line 178
The final question, we didn’t see the Table 1 and Table 2 in the manuscript, the authors need
to add them in the next revised version.
Review for 10.1186/s12876-025-04108-2 (2025)

Title: The effect of neoadjuvant chemoradiation therapy in resectable pancreatic cancer was
independent of intratumoral vascularization
Version: 4 Date: 16 May 2025
Reviewer's report:
Summary of the Manuscript:
This study investigates whether the enhancement patterns observed on CH-EUS are predictive of
the efficacy of NACRT in patients with resectable pancreatic cancer. Patients were classified into
three vascularization pattern groups, and outcomes including histological response, recurrence-
free survival, and overall survival were analyzed. The study concludes that NACRT efficacy is
independent of vascularization pattern.
Major Comments:
1. Justification of Research Question and Background: Elaborate on the biological  mechanism
through which radiotherapy may overcome fibrotic, hypovascular barriers.
2. Study Design and Population: Provide a power calculation and consider reporting baseline
characteristics by CH-EUS group with significance values.
3. CH-EUS Classification and Interobserver Agreement: Include more detail on how
enhancement was rated and describe training/calibration procedures.
4. Outcome Measurement and Statistical Analysis: Specify use of multivariate Cox regression
and include confidence intervals for survival curves.
5. Interpretation and Discussion of Results: Clarify whether NACRT truly renders CH-EUS
patterns irrelevant or if there are other plausible explanations.
6. Literature Contextualization: Expand comparison with other modalities and trials, such as
PREOPANC and JASPAC.
Minor Comments:
1. Abstract: Include group sizes, outcome metrics, and p-values.
2. Figures & Tables: Annotate Figure 1 and add risk tables/CI bands to Figure 4.
3. Terminology Consistency: Define 'isovascular' and 'hypovascular' early.
4. Grammar and Language: Correct minor grammatical issues throughout.
5. Ethical Statement: Add brief note on informed consent for data use.
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 2 Date: 25 Aug 2024
Reviewer's report:
Abulitifu and colleagues evaluated in a randomized trial the effects of combining UDCA with
vitamin D in treating patients with PBC. The aim of the study is interesting but several major
issues should be addressed to render the study feasible for publication
Major Criticisms:
-Study population in not adequately described.
For example, it is unclear how many patients were responder to UDCA at enrollment (see
enrollment criteria, i.e., page 5, line 85:  “the patients must have completed at least 2 years
of treatment”). This point is very relevant since, from the introduction of UDCA therapy, new
treatment strategies are mainly focused on PBC patients non responder or intolerant to UDCA.
In addition, it is not reported the number of patients who had liver cirrhosis at enrollment.
-Data exposition is confused, difficult to follow and needs a substantial improvement.
In the text no mean or median values are reported, while in figures 2, 3 and 4, it is very difficult
to read such values; also units of measures are not clearly indicated. By a logical point of view,
figure 3 and the paragraph starting from lines 164-165 should precede figure 2 and the paragraph
starting from lines 148-151. I suggest to delete figures 5 and 8 since the data have been already
reported in the text. Figure 7 is almost impossible to understand and these data may appear in a
table where also units of measures should be clearly indicated.
-The discussion need to be shortened.
In the first part of this section, data already reported in the result section are repeated rather
than discussed.
Other points:
Abstract: Lines 32-34 is a repetition of the sentences reported in lines 17-19
Methods: evaluation of non-invasive detection of hepatic fibrosis needs some more details
Results: Lines 206-209 is a repetition of sentences already reported in the method section (lines
101-105)
Discussion: lines 240-242 is a repetition of sentences already reported in the method section
(lines 101-105) and in the result section (lines 206-209)
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 2 Date: 09 Mar 2025
Reviewer's report:
Abulitifu Y et al conducted a randomized interventional trial for PBC patients to evaluate the
efficacy of vitamin D as the combination agent to improve treatment response of UDCA. Overall,
the protocol and presentation lacked scientific rigorousness and quality, being required for the
report of clinical trial.
Major concerns;
1. Introduction, Page 3, lane 19: male to female ration should be updated to previous literatures.
2. Introduction, Page 4, lane 6-8: Two sentences are redundantly and very vaguely written.
3. Introduction, Page 4, lane 14: What does it mean late stage UDCA therapy?
4. Endpoints: Primary, secondary, tertial, and surrogate endpoints should be defined clearly.
5. Endpoints: What definition were implemented for the improvement of symptoms, including
itch and malaise?
6. Methods: After the second allocation, followed by randomization, surrogate endpoints were
compared between experimental and control groups. What was the aim for such comparison?
Was it to evaluate the difference in the efficacy of vitamin D between the 1st and the 2nd year
of UDCA treatment?
7. In Figure 4-8: Groups in comparison for statistical analysis were hard to be realized. All
figures should be completely revised to give readers clear understanding.
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 2 Date: 30 Mar 2025
Reviewer:  Dawei Ding
Reviewer's report:
Reviewer
Decision: major revision
Dear Dr Zhang,
Your manuscript, "The effectiveness of combining ursodeoxycholic acid with vitamin D in
treating patients with primary biliary cholangitis and its impact on hepatic fibrosis",
has now been assessed.
1 Why use Paris-I and Toronto criteria to assess biochemical responses? These two evaluation
criteria are relatively lenient, and the current treatment targets for PBC patients are ALP (e.g.,
upper limit of normal) and bilirubin (e.g., 0.6 is the upper limit of normal) to lower levels?
2 Does the section 'Changes in clinical symptoms, biochemical and immunological indicators,
and liver stiffness values before treatment in the experimental and control groups' present
baseline data? If so, why is the term 'changes' used? If it is indeed baseline data, I believe it should
be placed before the section 'The study analyzed changes in clinical symptoms, biochemical and
immunological indexes, and liver hardness values before and after treatment in both the test and
control groups.'
3 Is there a difference in the anti-gp210 antibody positivity rate between the two groups at
baseline, given that anti-gp210 antibodies are associated with the prognosis of PBC patients?
4 How is the sample size determined for each group? Why do you think the sample size in each
group is sufficient?
5 A prospective study of initial combination therapy with fenofibrate (PMID: 36892506.) The
primary outcome was the biochemical response rate (based on the Barcelona criteria) at 12
months. In the UDCA-fenofibrate group, 81.4% (69.9%-92.9%) of patients achieved the primary
outcome, compared to 64.3% (51.9%-76.8%) in the UDCA-only group (P = 0.048). In this study,
after 1 year of treatment, the UDCA-vitamin D group showed an 86.7% biochemical response
rate, while the UDCA-only group had 63.3%. The response rate in the UDCA-vitamin D group
was slightly higher than in the UDCA-fenofibrate group. Do you believe vitamin D could replace
fenofibrate? Or might combining vitamin D with fenofibrate yield even better results? Based
on our center’s experience, adding vitamin D may not improve the biochemical response rate
compared to UDCA monotherapy.
6 We recommend that the discussion section focus on the implications of this study findings and
their clinical significance for the management of PBC patients.
Dawei Ding
Xijing Hospital of Digestive Diseases, The Air Force Military Medical University
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 4 Date: 19 May 2025
Reviewer:  Dawei Ding
Reviewer's report:
My review comments have been addressed. I think the article is acceptable for publication.
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 4 Date: 26 May 2025
Reviewer's report:
The authors did significant work to improve the paper  but some additional  changes are needed
to render the manuscript acceptable for publication.
1) In the Abstract and in the Result section it shoud be clearly stated where data description
come from the second year of the study  and after the second randomisation .
It should be added a sentence like " In the second year of the study  after the second
randomisation" in page 3, line 45 before "the response rate........".
Similarly  in the Result section , page 14, line 233. The same also in  the legend of table 6
2) Patients and methods. It should be clearly stated that in both inclusion and exclusion criteria
several points refer to inclusion or exclusion from the analysis, i.e, inclusion criteria #3 and #4
and exclusion criteria #5 and #6. Therefore, also the flowchart for patient selection reported in
figure 1 should be  changed.
3) In table 4 and table 6, where  the two study groups are compared , the changes from baseline
should be reported, rather than the absolute values
4) All the tables should be evaluated independently from the text. Therefore it should be clearly
indicated when data are expresses as  mean +/- SD rather than median (Q25, Q75).
Minor Points
a) Page 7, lines 131 and 132. The English language appears to be inadequate
b) Table 1 : "% of obese patients" instead of "BMI(Obese), kg/m2, n(%)"
Review for 10.1186/s12876-025-04118-0 (2025)

Title: The effectiveness of combining ursodeoxycholic acid with vitamin D in treating patients
with primary biliary cholangitis and its impact on hepatic fibrosis: A Randomized Trial
Version: 5 Date: 25 Jun 2025
Reviewer's report:
My review comments have been largely addressed.
The authors have added  a new table  (table 6) to  compare baseline characteristics between the
UDCA + vit D and UDCA monotherapy subgroups following the secon randomization.
In my opinion,  tabulation of changes (or % changed) would render much clear the exposition
of the data.  In any case this does not represent a major concern and the paper may be acceptable
for publication  with some language revision.
Review for 10.1186/s12876-024-03542-y (2025)

Title: Platelet Derived Growth Factor Receptor-# as a Non-Invasive Biomarker for Liver
Fibrosis Prediction in Diabetic Non-alcoholic Fatty Liver Disease
Version: 1 Date: 15 Oct 2024
Reviewer:  Panagiotis Tsibouris
Reviewer's report:
MAFLD should replace NAFLD and definitions should be accordingly adapted Abstract A nitch
should be provided about PDGFR# and liver steatosis Methods MAFLD should be excluded in
controls and the way of MAFLD exclusion should be provided Since MASLD excludes alcohol
consumption MetFLD is used for low alcohol consumption, alcohol consumption should be
excluded Definitions of underlined comorbidities should be provided HbsAg is not sufficient
to excluded HBV infection HbcAb and antiHbs are required Could results for F3 and F4 be
presented as well Statistics Non-parametric score utilized should be defined Had authors used
all these tests? In such a case definition of when each test was applied should be provided
Authors should point out why they have selected the cut off points they have used Analysis
in too small samples are dangerous Results significant differences of demographic and clinical
characteristics between patients and controls should be presented in the text and numerical values
as well as p values should be provided  Multivariated analysis in non diabetic patients should
be performed as well unless size of the population is not sufficient to preform it possibly one
analysis for the whole population would be advisable
Review for 10.1186/s12876-024-03542-y (2025)

Title: Platelet Derived Growth Factor Receptor-# as a Non-Invasive Biomarker for Liver
Fibrosis Prediction in Diabetic Non-alcoholic Fatty Liver Disease
Version: 2 Date: 01 Nov 2024
Reviewer:  Panagiotis Tsibouris
Reviewer's report:
I think all changes requested have been made. Thus the document is ready for publication I have
to congratulate the authors
Review for 10.1186/s12876-024-03542-y (2025)

Title: Platelet Derived Growth Factor Receptor-# as a Non-Invasive Biomarker for Liver
Fibrosis Prediction in Diabetic Non-alcoholic Fatty Liver Disease
Version: 3 Date: 22 Nov 2024
Reviewer:  Amira A A Othman
Reviewer's report:
I want to extend my congratulations to all those involved in this work. All the required
amendments have already been made carefully and satisfactorily. I hope that the research will
be presented to science.
Review for 10.1186/s12876-025-04113-5 (2025)

Title: Early Acetaminophen Administration and Mortality Outcomes in Critically Ill Patients
with Cirrhosis: A Retrospective Analysis from the MIMIC-IV Database
Version: 0 Date: 21 Mar 2025
Reviewer:  Tarana Gupta
Reviewer's report:
1. In Fig 1, 3020 patients included in IPW cohort which are further subdivided without and with
APAP use (3126 and 3205) respectively. Please explain how this subgrouping numbers exceed
main group.
2. Authors have not mentioned the cumulative dose of APAP in patients. They have not
mentioned the indication for which APAP was used in cirrhosis as this is indicated for fever
and pain only.
3. APAP is a dose dependent hepatotoxic drug which may be cumulative if used over several
days in a patient with cirrhosis.
4. They should also mention the formulation and route like intravenous or oral APAP which was
used in these patients as bioavailability and dose differs significantly among different routes.
5. The discussion mentions higher mortality in patients with bilirubin >10 mg/dL. however,
supplementary table shows upper bound of bilirubin at 5 or 7 mg/dL. Please explain.
6. In routine clinical practice, APAP has a relative contraindication in patients with
decompensated cirrhosis with jaundice. The study should check as to why so many patients were
receiving APAP in this high risk population.
Review for 10.1186/s12876-025-04113-5 (2025)

Title: Early Acetaminophen Administration and Mortality Outcomes in Critically Ill Patients
with Cirrhosis: A Retrospective Analysis from the MIMIC-IV Database
Version: 0 Date: 25 Mar 2025
Reviewer's report:
I read with attention Fan et al's work. They suggest that early APAP use is associated with worse
prognosis in cirrhosis patients in ICU. The study is interesting with advanced methodology.
Some remarks can be nececassary nevertheless:
- APAP dose woud be interesting. Have you got these informations? Also, what are indications?
- Child-Pugh-Turcotte and MELD score are prognostic in cirrhosis, have you got data?
- In results, line 163, method description is unuseful.
- Line 248, the term primitive biliary cholangitis must replaced primitive biliary cirrhosis.
Review for 10.1186/s12876-025-04113-5 (2025)

Title: Early Acetaminophen Administration and Mortality Outcomes in Critically Ill Patients
with Cirrhosis: A Retrospective Analysis from the MIMIC-IV Database
Version: 1 Date: 17 May 2025
Reviewer's report:
I read with attention corrections and answers from authors. I don't have any commentary except
concerning Acetaminophen doses: It would be more pertienent to choose 3000 mg for excess
instead of 4000.
Review for 10.1186/s12876-025-04111-7 (2025)

Title: Predictive Role of the Albumin-Bilirubin Score in ICU Patients with Cirrhosis and Sepsis:
Insights from a Large Retrospective Cohort
Version: 0 Date: 30 Apr 2025
Reviewer:  Iliana Mani
Reviewer's report:
This is an interesting study examining prognostic significance of ALBI score in cirrhotic patients
with sepsis. Although of clinical interest, there are several limitations in in its current form.
Major comments:
• Liver failure should be diagnosed based on well-established criteria like EASL or APASL. The
definition provided in supplementary material is rather general, making diagnosis questionable
(“Elevated Liver Enzymes: Significant increases in serum alanine aminotransferase (ALT)
and aspartate aminotransferase (AST), indicating liver cell damage. Elevated Bilirubin Levels:
Serum bilirubin levels above the normal reference range, which is a direct marker of impaired
liver excretion. Hypoalbuminemia: Low serum albumin levels, reflecting the liver ’ s reduced
synthetic capacity”
• The incidence of fungal infections is much higher than that reported in the literature.
[Fernández J, Piano S, Bartoletti M, Wey EQ. Management of bacterial and fungal infections
in cirrhosis: The MDRO challenge. J Hepatol. 2021 Jul;75 Suppl 1:S101-S117. doi: 10.1016/
j.jhep.2020.11.010]. Which criteria were applied for the diagnosis of fungal infections?
• Multivariate analysis-model 3. Authors used as covariates paltelets and creatinine but also
SOFA score. The above parametres are parts of the SOFA score. Inclusion of highly correlated
variables in multivariate analysis leads to multicollinearity problems making interpretation of
results problematic.
• To further support the statement that ALBI is a usefull prognostic tool in cirrhotic patients wih
sepsis, authors should compare its prognostic accuracy to this of other well-established markers,
like MELD, ACLF-score, SOFA score. ROC curves should be provided and compared for the
above parameters.
• Lack of a validation cohort should be added in study limitations.
Minor comments:
• Page 8, line 78: Instead of “liver-related diseases” authors could use “complications”
• Table 1 and Supplementary table 1:
- Liver failure, encephalopathy, ascites and variceal bleeding should be categorized separately
as there are complications of liver disease and not comorbidities.
Review for 10.1186/s12876-025-04111-7 (2025)

Title: Predictive Role of the Albumin-Bilirubin Score in ICU Patients with Cirrhosis and Sepsis:
Insights from a Large Retrospective Cohort
Version: 1 Date: 26 May 2025
Reviewer:  Iliana Mani
Reviewer's report:
Dear Editor
Authors addressed most of my concerns adequately. However, I have some further comments
to make.
#ajor comments:
• Table 1 :
- Septic shock should not be included in comorbidities
- Heart failure is not a complication of cirrhosis. Please rephrase as cirrhotic cardiomyopathy has
specific diagnostic criteria that cannot be examined in the current study given its retrospective
design.
• Supplementary table 1: Complications of liver disease are listed as comorbidities although this
is not accurate.
• Table 5: Please add p value for the comparison between ROC curves
Minor comments:
#able 5: Please correct “Septicity”