JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-03908-w (2025)

Title: Sphincter saving surgery for failed organ preservation after a Neoadjuvant therapy and
Radiation boost : A Surgeons Perspective
Version: 1 Date: 25 Mar 2025
Reviewer's report:
Thank you for writing this interesting article. Overall, I do think a severe revision is necessary.
To me it is still not clear what the reason was for giving certain patients a brachytherapy boost.
It was highly individualized as the authors describe, yet this introduces an enormous selection
bias after which fair comparison between the two groups (with or without brachytherapy) is not
possible. On the basis of what I read I don't believe the two groups can be compared, so the
paper should be come more observative.
There is no information on the brachytherapy boost (dose, technique, volume irradiated). As
this is essential to be able to interpret relevant toxicity, it is extremely necessary to include this
data in the paper.
Please take care to use the correct names for certain treatments. For example, "Contact radiation"
is not correct, it should be termed Contact brachytherapy (CXB). "Brachy boost" is also not a
professional term.
Revision of the entire text is warranted as the grammar and sentence structure is not adequate
now.
Review for 10.1186/s12876-025-03967-z (2025)

Title: Effect of pemafibrate in reducing intestinal long-chain fatty acid absorption and hepatic
fibrosis in metabolic dysfunction-associated steatohepatitis rats
Version: 0 Date: 05 Mar 2025
Reviewer's report:
The manuscript by Okada et al., examines the role of pemafibrate on intestinal lipid metabolism
in the context of a rat model of MASH.  The study design is straightforward and well controlled.
The data support reduced lipid accumulation in the intestinal epithelium and a modest reduction
in fat absorption that is associated with a reduction in mRNA levels of lipid metabolizing and
transport enzymes in the intestine.  However, there are a number of limitations that reduce
enthusiasm for acceptance of the manuscript.
Major concerns:
1) The analysis is limited to a measure of fat absorption, intestinal and liver histology and rtPCR
of a handful of genes implicated in intestinal lipid handling and liver phenotypes.
2) Gene expression of markers expected to increase with PPAR alpha agonism in both liver and
intestine would give reviewers confidence that the drug is affecting this transcriptional pathway
as previously published (i.e fatty acid oxidation enzymes).  As it is all target genes are either
reduced or unchanged in fibrate-treated rats.
3) Confirmation of changes in lipid metabolizing enzymes at the protein level, particularly
CD36.
4) The effects of pemafibrate on liver collagen deposition and a-SMA levels are expected and
may or may not have any connection to the observed phenotypes in the intestine, which is the
focus of the manuscript as outlined in the background and title.
5) The reduction in fat absorption as determined by mass measurements is ~1%.  It is difficult
to know if such a difference is biologically relevant in the setting of a diet composed of 27%
palm oil and the development of MASH phenotypes.
6) The measurement of fat absorption is not state-of-the-art and would be strengthened by the
use of a non-absorbable marker.
7) The accumulation of lipid in Oil Red O positive areas in the intestinal epithelium is interpreted
as evidence of reduced lipid absorption.  Firstly, the reduction in staining appears to be far greater
than the reduction in fat absorption (1%).  Secondly, the reduction could reflect more rapid
chylomicron assembly and secretion or increased fat oxidation within the intestinal epithelium
following fibrate treatment.
8) The suppression of intestinal CD36 by pemafibrate is somewhat puzzling, but not necessarily
incorrect.  A host of transcription factors have been implicated in the upregulation of CD36,
including PPAR alpha.  Admittedly, CD36 has been more heavily studied in other cell types
which may not reflect regulation in the intestinal epithelium.  In the present study, mice are fed a
diet containing palm oil, cholesterol, and cholate.  All of which may influence CD36 expression
via PPARs, LXR, and NF-KB.
Minor Concerns:
1) The diet should be better described and percent lipid expressed in kCal.
Review for 10.1186/s12876-025-03983-z (2025)

Title: Feasibility and predictors of same-day discharge following endoscopic submucosal
dissection for early esophageal cancer
Version: 1 Date: 25 Apr 2025
Reviewer:  Xun Lu
Reviewer's report:
The authors reported on feasibility and predictors of same-day discharge following endoscopic
submucosal dissection for early esophageal cancer.
Overall, this study has a large number of cases and is a meaningful report.
However, some revisions are necessary.
1.Details of ESD procedures and postoperative management should be provided in Methods,
such as when to drink water properly, proton pump inhibitor therapy, and antibiotics, etc.
2.Some sentences should be rewritten in Discussion.
Review for 10.1186/s12876-025-03983-z (2025)

Title: Feasibility and predictors of same-day discharge following endoscopic submucosal
dissection for early esophageal cancer
Version: 1 Date: 28 Apr 2025
Reviewer's report:
The authors presented a study on the feasibility and predictors of same-day discharge following
endoscopic submucosal dissection for early esophageal cancer.
This manuscript is well written and organized. However, this manuscript has few novelties.
Below are the comments and questions.
Major
1. This study focuses on the clinical characteristics to evaluate the feasibility and risk factors
of same-day discharge following esophageal ESD. However, to properly assess feasibility, the
post-discharge clinical course (e.g. symptoms, aspirated pneumonia, the presence of visiting
emergency care unit and readmission to the hospital) should also be discussed.
2. Since the type and dose of sedation used during ESD may influence discharge timing,
these details should be reported. In addition, from previous studies, alcohol abuse is correlated
with unsuccessful sedation. This suggests more sedation needs in the patients with alcohol
abuse, which may affect the total dose of sedation. This hypothesis should be mentioned in the
discussion section.
3. The rate of intraoperative bleeding in this study appears to be higher than that reported
in the previous studies on esophageal ESD. As intraoperative bleeding and perforation also
may influence the decision of SDD following ESD, definition of these terms should be clearly
provided in the manuscript.
Minor
1. In the result section, the number of patients with early esophageal cancer who underwent ESD
was 168. However, in Figure1, the number of patients with early esophageal cancer was 168.
The sentence in the manuscript should be corrected.
Review for 10.1186/s12876-025-03979-9 (2025)

Title: The prognostic role of albumin-bilirubin grade in the mortality of extrahepatic
cholangiocarcinoma patients
Version: 0 Date: 09 Feb 2025
Reviewer's report:
Comments to the Author
The article titled " The prognostic role of albumin-bilirubin grade in the mortality of extrahepatic
cholangiocarcinoma patients"
This article is commendable and showcases strong writing skills. The authors merit
recognition for their contributions. Nevertheless, it is suggested that the subsequent notices/
recommendations enhance the caliber of this endeavor.
1. In the Abstract and the main text, the grade of ALBI score in grade 2 should be scaled from
lower to upper limit.  grade 2: #1.39 to #2.60 should change to > #2.60 to # #1.39.
2. In Abstract, the unit of laboratory results should be added to standardized reports (AST, WBC)
and recheck all abbreviated terms are defined the first time in abstract and main text: ERCP,
AST, WBC, INR.
3. Introduction, suggest adding incidence, survival rate of cholangiocarcinoma in Iran, are
different or the same as the global basis.
4. The author should specify whether the bilirubin and other liver function test are evaluated after
drainage, after chemotherapy or before surgery, history infection that affect the WBC, TBIL
level and which methods of drainage after tissue/cytology were received. Only internal drainage
by stent?
5. In the Method, the author should correct the format of ALBI score calculation:
from 0.66 × log10 TBIL (µmol/l)-0.085 × ALB (g/l) to
(0.66 × log10 TBIL [µmol/L]) + (#0.0852 × albumin [g/L])
6. In the Statistical Analysis, please check the symbol. P>0.05 was considered significant in all
tests should be < (less than).
7. Explain the definition of the types of eCCA, in the table the author divided into distal,
proximal, hilar type. How about the surgical procedure, in all types have done by Whipple
operation (Pancreaticoduodenectomy)? No liver resection?
8. In the table, the unit of laboratory results should be added to standardized reports. For example:
ALT (U/l), ALB (g/l), TBIL (µmol/l).
9. The author should mention other main factors that affect survival rates. What was the
pathological stage (size, nodal status, metastasis status) of these patients?  postoperative in-
hospital mortality? Viral hepatitis? Effect on type chemotherapy was used in patients, induced
transaminitis? the chemotherapy in the table was pre or postoperative chemotherapy?
10. Please check spelling: grade in the figure 2
: 2nd paragraph of discussion: Differences in characteristics of patient population (such as sex,
age, economic status, stage of cancer…).
Review for 10.1186/s12876-025-03979-9 (2025)

Title: The prognostic role of albumin-bilirubin grade in the mortality of extrahepatic
cholangiocarcinoma patients
Version: 0 Date: 15 Feb 2025
Reviewer's report:
Well presented case. It will add to the current literature. It will add useful clinical information
for hepatologists.
Review for 10.1186/s12876-025-03979-9 (2025)

Title: The prognostic role of albumin-bilirubin grade in the mortality of extrahepatic
cholangiocarcinoma patients
Version: 0 Date: 20 Feb 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The introduction references several studies that support the significance of liver function in
predicting outcomes for iCCA and eCCA, but a bit more detail on these studies could be helpful.
For instance, elaborating on why ALBI is superior or more reliable than CP in some situations
would provide stronger reasoning for its inclusion in the study.
-While the introduction provides a solid rationale for the study's aim, it could benefit from more
detail on the limitations of the existing literature on ALBI in eCCA patients. Specifically, how
the findings from studies on iCCA might not translate to eCCA, and why this justifies the need
for further research.
-The introduction mentions the poor prognosis of eCCA patients but could delve a bit deeper
into the specific challenges in predicting survival for this group. A more explicit mention of
the difficulty in predicting mortality and the potential consequences for clinical management
(treatment decisions, prognostication, etc.) could strengthen the argument for why mortality
prediction is an important goal of the study.
-The explanation of the ALBI score formula and its interpretation is solid, but more clarity on
how the score compares to other liver function assessments (e.g., CP) in predicting mortality or
overall survival for eCCA patients would be helpful. Additionally, a brief explanation of why
certain clinical markers (e.g., liver enzymes, WBC, INR) are chosen for the study would be
useful to tie them to the broader context of liver dysfunction in CCA.
-While the study shows a significant correlation between ALBI grading and survival, the
explanation of how ALBI grade functions as a predictor of liver function could be expanded.
Providing more insight into why ALBI might be a better marker than other scores, such as CP,
in this cohort could strengthen the argument for its clinical relevance.
-While the discussion mentions confounding variables and biases due to the retrospective design,
it could go further in discussing the specific factors that could have confounded the results. For
example, were there any biases in how patients were selected for Whipple surgery or how their
liver function was assessed preoperatively? Further detail on potential confounders would add
more nuance to the discussion.
-Although the discussion does a good job of addressing ALBI’s role, it could benefit from a
bit more depth in comparing ALBI with other liver function tests in eCCA specifically. For
example, how does ALBI compare to newer markers like MELD or serum biomarkers in terms
of predictive power for mortality in eCCA?
Review for 10.1186/s12876-025-03979-9 (2025)

Title: The prognostic role of albumin-bilirubin grade in the mortality of extrahepatic
cholangiocarcinoma patients
Version: 1 Date: 30 Mar 2025
Reviewer's report:
This article was satisfactory revised after suggestion. Nevertheless, it is suggested that some
recommendations enhance the caliber of this endeavor.
1. Explain the definition of the types of eCCA, in the table the author divided into distal,
proximal, hilar type. How about the surgical procedure, in all types have done by Whipple
operation (Pancreaticoduodenectomy)? No liver resection?
Reply by the author(s) : eCCA consists of perihilar cholangiocarcinoma and distal eCCA
(involving all parts of the common bile duct). Based on the site of involvement, patients
underwent either pancreatoduodenectomy or segmental biliary resection. Patients with
perihilar CCA who underwent en bloc resection of the bile duct, with or without regional
lymphadenectomy and with or without lobectomy, were included in the study. Patients with
perihilar involvement who underwent liver transplantation were excluded from the study.
Comments:  In the inclusion criteria, the author already removed the specific operative procedure
“Whipple operation” and replaced by “surgery”.
To complete this statement by adding the exclusion criteria in study population (Page 4 Line 6) :
Patients with perihilar involvement who underwent liver transplantation were excluded from
the study.
Review for 10.1186/s12876-025-03986-w (2025)

Title: Better diagnostic accuracy for GERD observed with the new MNBI cutoff: An
observational study in Vietnam
Version: 3 Date: 29 Mar 2025
Reviewer's report:
Dear Authors,
I have read with great interest your work entitled “Better diagnostic accuracy for GERD observed
with the new MNBI cutoff: An observational study in Vietnam”. An important strong point is
that the study is the first study in Vietnam in which 24-hour esophageal pH monitoring was used
to diagnose GERD.
In your study you underline the diagnostic usefulness of the novel MNBI thresholds in
identifying GERD. It is known that MNBI thresholds in identifying GERD are variable in the
different populations. It varies across studies and may be lower in Asia than in Europe, but
your study confirms the data literature thresholds in Vietnam population: the MNBI value is
significantly lower in patients with abnormal AET and the percentage of MNBI >2500 Ohms
was 2.9% in patients with abnormal AET. In fact, you confirm that the new cutoff value of 1500
Ohms has high sensitivity and specificity in diagnosing GERD.
1. Why did you use Chicago classification version 3? You have excluded patients with EGJ-
OO but the manometric diagnostic criteria differ from Chicago 3 to Chicago 4 classification. I
suggest re-evaluating your study population using Chicago classification version 4 or excluding
only patients with EGJ-OO diagnosis if they have a confirming radiogram. Your choice must be
explained in the text and the Chicago classification version 4 must be added in the bibliography.
2. In your study’s population, 80 patients (60.2%) had erosive esophagitis, predominantly LA
grade A (93.8%). Did patients undergo endoscopic examination off PPI therapy? This data must
be added to the text.
3. You use the term “hypomotility”. Is it possible to use a more specific terminology?
4. You haven’t described EGJ types. Can you put them on your table?
5. I don’t understand in your text if, in the inconclusive group, MNBI thresholds are useful to
rule on or off GERD diagnosis.
6. Did patients undergo pH-impedance examination off PPI therapy?
7. In the figure 1 (part b), I would put patients with LA grade A esophagitis with NERD group,
considering that LA grade B, C and D esophagitis are diagnostic for GERD (Lyon consensus
v.2).
Review for 10.1186/s12876-025-03986-w (2025)

Title: Better diagnostic accuracy for GERD observed with the new MNBI cutoff: An
observational study in Vietnam
Version: 3 Date: 30 Apr 2025
Reviewer's report:
THis is a monocentric retrospective analysis of a limited samples of patients underwent upperGI
evaluation in GERD suspect. The study has several limitations that decrease the enthusiasm in
the conclusions drawn by authors. My comments:
- Line 34: were patients with an already proven GERD (as stated by authors),  on or off PPI
therapy during exam? Specify, while this would change parameters.
- Line 39: How many patients did you excluded with major motility disorders, and why not
reassessing with Chicago 4.0, where a lot of previous diagnosis of EGJ-OO would have been
rediscussed.
- Results sections: Did you also stratified in the GERD phenotypes according to Lyon 2.0, how
was MNBI in these classes? How was the clinical assesment with questionnaires related to
MNBI? Were patients with hypomotility/LES hypotonia with lower MNBI?
- Line 63: why according to old Lyon consensus?
- Line 66: I would add "additionally", because is not included in diagnosis criteria but for
research purposes
- Line 85: I would just say that had no erosions, instead of GERD-related abnormalities
- Line 111: DIscussion should be expanded to more results reported in the tables.
- Line 131: "Frazzoni"
Review for 10.1186/s12876-025-03944-6 (2025)

Title: Marked mucosal lipid shifts in treatment refractory inflammatory bowel disease: a
lipidomic study
Version: 0 Date: 02 Aug 2024
Reviewer's report:
Øystein Kittel Moe et al. evaluated mucosal lipid shifts in treatment refractory inflammatory
bowel disease. This is a very interesting area of research with the potential to identify predictors
of response/new targets for treatment. However, there are some limitations that should be
addressed:
1.      The authors mention various inflammatory and treatment pathways in the background and
discussion sections that do not seem to pertain directly to your data on lipids (eg JAK/STAT and
S1P pathways as well as PEMT, PDTSS2, and ELOVL3). Consider omitting this information
or clarify how it pertains to your findings.
2.      While it is useful to have information on patients treated with vedolizumab, it is difficult to
draw any conclusions from the data you have with only 2 patients in this study on vedolizumab.
3.      It would be clinically useful to know about other variables that can affect mucosal
lipid levels such as serum lipid levels, BMI, and nutritional status (perhaps evaluated through
prealbumin levels or other nutritional markers) and if these could affect the results.
4.      Please expand on the choice to use anti-TNF mucosal transcript as a marker for disease
remission as this is not a commonly used measure or standardized treatment goal.
5.      More information is needed regarding sampling location such as large or small bowel which
could affect baseline lipid levels as well as targeted biopsies for those patients in remission.
Were biopsies taken from areas where these patients were known to have the most severe disease
in the past (I.E. rectum in patient with UC proctitis in remission)?
6.      It is unclear why there was no significant difference between lipid profiles of refractory UC
patients and those in remission. Further discussion of possible reasons behind this is indicated.
Thank you again for your submission. This area of study holds promise, and I hope these
clarifications will serve to strengthen the message of your research
Review for 10.1186/s12876-025-03944-6 (2025)

Title: Marked mucosal lipid shifts in treatment refractory inflammatory bowel disease: a
lipidomic study
Version: 3 Date: 23 Mar 2025
Reviewer's report:
I would like to thank the authors for taking the time to respond to all the questions.
As the authors acknowledge the potential for inaccurate estimation of the SES-CD score, I would
strongly recommend avoiding the use of SES-CD in this context. An alternative approach—
though less standardized—such as categorizing endoscopic findings as mild, moderate, or severe
based on the physician’s assessment, may be more appropriate for endoscopic reports in your
specific situation.
Review for 10.1186/s12876-025-03938-4 (2025)

Title: Worldwide burden and cross-regional health inequalities of high BMI-attributable
colorectal cancer by gender from 1990 to 2021, with predictions through 2041
Version: 0 Date: 21 Mar 2025
Reviewer's report:
1. in the Methods, please provide  the definition of SDI measure, and how it is calculated.
2. in the Methods please  mention the R package that was used for data analysis.
3. the title is: Worldwide burden and cross-regional health inequalities of overweight-
attributable colorectal cancer by gender from 1990 to 2021, with predictions through 2036. I
would suggest that you calculate the attributable fraction of overweight for CRC.
Review for 10.1186/s12876-025-03938-4 (2025)

Title: Worldwide burden and cross-regional health inequalities of high BMI-attributable
colorectal cancer by gender from 1990 to 2021, with predictions through 2041
Version: 1 Date: 21 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
the responses are satisfactory
Review for 10.1186/s12876-025-03970-4 (2025)

Title: Clinical efficacy of TACE using coil or gelatin sponge combined with targeted therapy
in the treatment of giant hepatocellular carcinoma with arterioportal fistulas
Version: 0 Date: 24 Mar 2025
Reviewer:  Sirui Fu
Reviewer's report:
This is an interesting study comparing coil or gelatin sponge combined with targeted therapy
for giant hepatocellular carcinoma with arterioportal fistulas. Dr. Wu et.al provided evidence
in the efficacy of HCC treatment decision making. However, there are some questions to be
further answer:
1. In the background, the author said “The treatment of HCC combined with cancer thrombi and
arteriovenous fistula is complex, and the prognosis is worse compared to that of HCC alone”,
please give detailed description for the “complex”, and explain why theoretically TACE should
be combined with targeted therapy.
2. In the materials and methods section, the author should declared between OS and PFS, which
one is first outcome, and which is the second outcome.
3. In the Results section, the table 3 showed that the proportion of liver cirrhosis is very low,
considering most HCC were caused by HBV in China. So the cirrhosis is diagnosed by biopsy
or it is just radiological signs for cirrhosis, the author should declare it.
4. In the Results section, in the survival analysis and associated prognostic factors, OS is usually
expressed by median and interquartile range, not mean and SD.
Review for 10.1186/s12876-025-03970-4 (2025)

Title: Clinical efficacy of TACE using coil or gelatin sponge combined with targeted therapy
in the treatment of giant hepatocellular carcinoma with arterioportal fistulas
Version: 1 Date: 24 Apr 2025
Reviewer:  Sirui Fu
Reviewer's report:
All questions have been well answered
Review for 10.1186/s12876-025-03968-y (2025)

Title: The Current Status and Prospects of Gut Microbiota Combined with PD-1/PD-L1
Inhibitors in the Treatment of Colorectal Cancer: A Review
Version: 1 Date: 24 Feb 2025
Reviewer:  Guojun Tong
Reviewer's report:
Dear Author,
I am glad to review the paper titled “The Current Status and Prospects of Gut Microbiota
Combined with PD-1/PD-L1 Inhibitors in the Treatment of Colorectal Cancer: A Review”.
My comments are as follows:
1.It is general written which should be polished bu English institution for further reviewing.
2.The abstract is too long, and should be simplified. And the words of abstract should be under
300 words.
3.After the sentences of “In recent years, the growing body of research on the gut microbiome,
with its crucial role in various diseases including those of the nervous, endocrine, and urinary
systems, has led to its recognition as the "second genome" of humans, playing an indispensable
role in health and disease.”,Please add reference.”.
4.It was a good conception and well constructed.
5.The methods was good and conclusions are confidential.
In a word ,My suggestion is minor revision.
Review for 10.1186/s12876-025-03968-y (2025)

Title: The Current Status and Prospects of Gut Microbiota Combined with PD-1/PD-L1
Inhibitors in the Treatment of Colorectal Cancer: A Review
Version: 1 Date: 04 Mar 2025
Reviewer's report:
Deng and colleagues present a review of an important topic in the management of colorectal
cancer (CRC) with immune checkpoint blockade (ICB): the role of the gut microbiome in
modulating these responses to therapy. Unfortunately  in CRC  there are limited reports of the
role of the gut or tumoral microbiome affecting the efficacy of response to therapy as reflected
by their review here. As such I worry that there are groupings of studies combining gut and
tumoral microbial profiles as well as pMMR and dMMR CRC tumors. It is unclear to me that
these groupings can and should be made and that it may cloud the understanding of each of
these distinct biological processes. Additionally much of the text reviews well defined biologic
processes and does not focus on their very important and nuanced question of the role of the
microbiome in modulating responses to ICB.
Major Points:
1) Response to ICB in CRC outside of the clinical trial setting is almost completely limited to
dMMR CRC. This important distinction is blurred throughout the manuscript and especially
importantly so in the introduction of the work which inappropriately may lead one to assume
efficacy of ICB across CRC subtypes. Throughout the manuscript this delineation needs to be
made more clear.
2) The methods presented are that of a structured and systematic review while the majority of the
text does not delve into the 8 preclinical and 5 clinical studies but instead discusses incomplete
reviews of various other biological processes instead of focusing on the role of the tumoral and
gut microbiome in driving heterogeneity in response.
3) Be careful throughout the text to delineate the tumoral and gut microbiome. These two distinct
communities engage tumoral and host biology through very different processes.
Minor Points:
1) The review of the role of the microbiome in CRC in the introduction is extremely limited
and frankly outside the scope of a review focused on its role in modulating response to ICB.
There are innumerable reviews of the microbiome in CRC and if it is reviewed a more thorough
review would certainly be necessary if one is going to the detail of noting individual bacteria
and researchers.
2) Non-english text is included in Figure 1 severely limiting one's ability to review this presented
English language manuscript. Furthermore the caption presented includes instructions to the
author using a templated form and should have been removed. This degree of oversight is
unacceptable and calls the overall work into significant question.
3) Why is the country of study included in the clinical but not animal studies table?
4) Review of the mechanism of action and resistance of ICB seems well outside the scope of
this review. Moreover these sections are again incomplete in their review.
Review for 10.1186/s12876-025-03968-y (2025)

Title: The Current Status and Prospects of Gut Microbiota Combined with PD-1/PD-L1
Inhibitors in the Treatment of Colorectal Cancer: A Review
Version: 4 Date: 14 Apr 2025
Reviewer:  Guojun Tong
Reviewer's report:
Dear authors and editor,
I am glad to review the revised paper titled “The Current Status and Prospects of Gut Microbiota
Combined with PD-1/PD-L1 Inhibitors in the Treatment of Colorectal Cancer: A Review”. It is
revised carefully point by point. I have no further comments.
My suggestion is acceptance.
Yours Sincerely
Guojun Tong
Review for 10.1186/s12876-025-03968-y (2025)

Title: The Current Status and Prospects of Gut Microbiota Combined with PD-1/PD-L1
Inhibitors in the Treatment of Colorectal Cancer: A Review
Version: 4 Date: 22 Apr 2025
Reviewer's report:
The authors did not adequately respond to reviews. I previously recommended rejection of this
manuscript and would re-iterate that point.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 0 Date: 04 Jan 2025
Reviewer:  Mohan Khadka
Reviewer's report:
In manuscript, I advise authors to look into the following points
1) In sentences 128 and 129: [From 2002 to 2023, the proportion of HTG-AP patients ranged
from 1.6% to 47.6%, showing an overall upward trend, though statistically nonsignificant
(P=0.1081)]
Comment:  As the data shows drastically so high difference in percentage from 1.6% in 2002 to
47.6% in 2023 with regard to increased proportion of HTG-AP, at a glance it looks significant
increase in incidence. Please kindly review the data analysis for significance.
2) Regarding definition of HTG- AP : Authors should mention the standard widely accepted
definition and also reason for differences across different guidelines which give more clarity
for readers.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 0 Date: 04 Jan 2025
Reviewer:  Serghei Covantsev
Reviewer's report:
Thank you for the possibility to review the manuscript titled: “A Systematic Review of the
Epidemiology and Risk Factors for Severity and Recurrence of Hypertriglyceridemia-Induced
Acute Pancreatitis”. The review is on a hot topic since acute pancreatitis is a complicated
condition and a major cause of morbidity and mortality. The systematic review is interesting,
however, requires several improvements:
-Please mention in the introduction section that acute pancreatitis is a potentially fatal condition
if it is severe. Also please mention that this is a risk factor for pancreatic malignancy. These
points are good arguments that make the condition even more important.
-Please comment why the study was limited to a systematic review without a meta-analysis.
This should be indicated in the material and methods section.
-There is no discussion of limitations at the end of the discussion section. One potential limitation
is that there is only one RCT included in the analysis, therefore there is some possibility of
unintentional bias. This is mentioned in the conclusion section. I would recommend transferring
this chapter.
-There is no discussion of risk factors for HTG-AP recurrence in the discussion section. I would
recommend expanding this section since comorbidities are a major risk factor in the development
and progression of the condition.
-The conclusions look more as discussion. The main conclusions of the analysis are indicated
in the abstract: “Smoking history, poor lipid control (TG > 3.1mmol/L), or recurrent
hypertriglyceridemia during follow-up were identified as potential predictors of HTG-AP
recurrence. Our findings indicate a stable global prevalence of HTG-AP within AP patients, but
a notable increase in China, possibly attributed to socio-economic and dietary factors.” I think
these are the main points that are important.
Overall this is an interesting and well-written study, please take into account the
recommendations in the spirit of improving the quality of the submission.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 0 Date: 06 Jan 2025
Reviewer's report:
Dear Authors,
I have reviewed your manuscript on hypertriglyceridemia-induced acute pancreatitis. While the
topic is undoubtedly of interest, I found several critical issues that need to be addressed to meet
the standards of a systematic review and meta-analysis.
1. The abstract lacks the concise synthesis of data typical in meta-analyses. It should reference
the statistical analyses performed, including p-values, measures of heterogeneity (e.g., I²), and
effect sizes with confidence intervals. The results presentation should be more quantitative and
less discursive.
2. The introduction should clearly articulate the hypotheses addressed by the study. Unlike
observational studies, systematic reviews require a well-defined hypothesis as it guides the entire
review process.
3. The search strategy needs more detail, particularly the inclusion and exclusion criteria used
to define hypertriglyceridemia-induced acute pancreatitis (HTG-AP) in the reviewed studies.
Moreover, provide comprehensive details on the data extraction methods and the tools used for
bias assessment in the methods section.
4. The results section should present a more robust quantitative synthesis, including
heterogeneity assessments and statistical comparisons using p-values.  A deeper analysis of
regional and temporal differences should be included, potentially through subgroup analyses or
meta-regressions.
5. The discussion should elaborate on the implications of the findings and include a critical
assessment of the study’s limitations in the context of existing literature.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 1 Date: 05 Mar 2025
Reviewer:  Serghei Covantsev
Reviewer's report:
The authors have made all of the necessary corrections.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 1 Date: 05 Mar 2025
Reviewer:  Mohan Khadka
Reviewer's report:
Dear Author. It seems that you have addressed my concerns and revised as per need.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 1 Date: 08 Mar 2025
Reviewer's report:
The article has been very well improved and can be accepted in the current form. Congrats to
the authors!
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 1 Date: 10 Mar 2025
Reviewer:  #ukasz Nawacki
Reviewer's report:
The authors present a systemic review of patients with hypertriglicerydemia induced acute
pancreatitis.
Overall, the manuscript has many grammar mistakes or missing words/letters, for example:
line 89 "he treatment strategy"
line 123 "only included" shouldn't it be "one included"
line 135 "included study basic information" - what included? I know that the data retriewed
included but without it the sentence is incomprehensible.
lines 155-158 the sentence is unintelligible
any many others. I recommend to recheck the manuscript.
I'm missing a point when was the string for the article searched - exact date.
I'm missing a point about the consent of the bioethical committee - why is it nopt applicable?
It's hard to compare studies with such wide range of HT-AP diagnosis criteria - in the table the
HTG definition is from: > 153 mg/dl through >500, > 1000, >1772, > 5000. In my opinion the
extreme ranges should be excluded because they are not any formal diagnostic criteria of any
international society.
Review for 10.1186/s12876-025-03954-4 (2025)

Title: A Systematic Review of the Epidemiology and Risk Factors for Severity and Recurrence
of Hypertriglyceridemia-Induced Acute Pancreatitis
Version: 1 Date: 10 Mar 2025
Reviewer's report:
I agree with the authors’ changes, and the article’s overall quality.
However, some relevant typos and English grammar errors along the whole text, especially in
newly introduced parts, require revision.
Review for 10.1186/s12876-025-03973-1 (2025)

Title: Clinical outcomes of endoscopic retrograde cholangiopancreatography after Billroth II
anastomosis: A comparison of gastroscope and duodenoscope
Version: 1 Date: 08 Apr 2025
Reviewer's report:
Dear author,
As far as I can see, your article is quite good. I don't have much to add as a correction. I think
it's successful.
Review for 10.1186/s12876-025-03973-1 (2025)

Title: Clinical outcomes of endoscopic retrograde cholangiopancreatography after Billroth II
anastomosis: A comparison of gastroscope and duodenoscope
Version: 1 Date: 11 Apr 2025
Reviewer:  Payam Behzadi
Reviewer's report:
Dear Author
Thank you for your manuscript submission. The manuscript is well-designed and well-
presented; however, a revision is needed as below:
1. Please do mention the number of males and females in both groups. Please do mention the
age range of the males and females in both groups.
2. Please do revise the tables content according to the comment #1.
3. Please do add the related statistical analyses according to comment #1.
4. Please do add the results of the  aforementioned statistical analyses to Results section.
5. Please do interpret the added statistical analyses to Discussion section.
6. There are some typo errors within the text.
Review for 10.1186/s12876-025-03973-1 (2025)

Title: Clinical outcomes of endoscopic retrograde cholangiopancreatography after Billroth II
anastomosis: A comparison of gastroscope and duodenoscope
Version: 2 Date: 21 Apr 2025
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Overall, the manuscript has been strengthened . While the retrospective design and limited
sample size remain unavoidable limitations, the transparency and detail provided in the revised
manuscript mitigate these concerns to a reasonable extent.
Minor Revision Suggestions:
-Ensure that all additions to the Discussion and Procedure sections referenced in the responses
are clearly reflected in the final manuscript.
-Consider tightening some of the language in the revised Limitations section for improved
readability and flow.
-If feasible, briefly mention any plans for future prospective or multicenter studies in the
Conclusion to emphasize the study’s role in guiding future work.
Review for 10.1186/s12876-025-03973-1 (2025)

Title: Clinical outcomes of endoscopic retrograde cholangiopancreatography after Billroth II
anastomosis: A comparison of gastroscope and duodenoscope
Version: 2 Date: 22 Apr 2025
Reviewer's report:
The authors have made corresponding changes or explanations to the revisions, and the authors
have also made substantive explanations or additions to some of the content we have requested,
and we believe that the current state of the manuscript has reached the level of publication.
Review for 10.1186/s12876-025-03973-1 (2025)

Title: Clinical outcomes of endoscopic retrograde cholangiopancreatography after Billroth II
anastomosis: A comparison of gastroscope and duodenoscope
Version: 2 Date: 28 Apr 2025
Reviewer:  Payam Behzadi
Reviewer's report:
Dear Author
Thank you for your rigorous revision.
Review for 10.1186/s12876-025-03982-0 (2025)

Title: Role of Liver Transient Elastography in Detecting Cirrhosis with Esophageal and Gastric
Varices and Evaluating Variceal Severity
Version: 1 Date: 06 Apr 2025
Reviewer:  Billy Siahaan
Reviewer's report:
first of all , congratulations for your research
i would like to comment about your study
1 .  could you describe what classification did you use for  varices grading on your research ?
2.  i think you should mention what health people ( control group) means in your research?  the
people with cirrhosis with out varices or healthy people with out any kind of disease?
3.  could you diverse in your subject , the etiology of cirrhosis , with or with out anti viral ,
because its should be  influence for your result .
4.  I also not so clear what kind of methodology that you use for this study , is this the
retrospective cross sectional study ?  what about the timeline between the endoscopy finding
and transient elastography evaluation ?  did at the same time or different time ? could you more
detail to explained your method
5. " success rate should be higher than 60%, the relative deviation should be less than 33% "  ,
as i know the relative deviation if you mean by that was interquartile range / median ( IQR/M)
should be below 30% not 33 %
6.  In your result i do not see the complete base line characteristic subject in your research.
Could you showed with a good table about variable that really important , for example Trombosit
count , child pugh score etc . Because i think it is very important to know what is the child pugh
category that dominant in your research ,
7. I  am a little bit hesitate about the result of specificity "100" for liver stiffness performance
related to diagnose cirrhosis and varices esophageal, could you explain where did you get this
outstanding number ?
Review for 10.1186/s12876-025-03982-0 (2025)

Title: Role of Liver Transient Elastography in Detecting Cirrhosis with Esophageal and Gastric
Varices and Evaluating Variceal Severity
Version: 1 Date: 10 Apr 2025
Reviewer's report:
Main comments:
1. There is only one author in this study, which is a bit incredible. Are there any other people
involved in this work? If so, it is recommended to add them to the list of authors or add the
acknowledgments.
2. In this study, a total of 136 patients were included, of which 25 had severe EGV. The number
of cases is small and the proportion is unbalanced.
3. Many tables in the manuscript are not standardized, please revise them.
Minor comments:
1. Introduction, first paragraph: Research reported an extremely high mortality rate (up to 25%)
of a first variceal bleed in cirrhotic patients. Please add citations.
2. Introduction: It should be supplemented to explain the necessity of confirming the presence
or absence of varicose veins in patients with cirrhosis and distinguishing different degrees of
varicose veins. Please explain in detail what are the specific differences in their treatment and
prognosis.
3. Methods, first paragraph: How was the control group determined? Is it in accordance with
randomization? Please compare with the cirrhotic patients without esophageal varices.
4. Methods Table 1: The table format is not standardized, the abbreviations need to be explained,
and the statistical methods for measurement data and counting data are not reasonable.
5. Results Table 2: There is no significant difference in laboratory indicators between the healthy
control group and the cirrhosis groups. Please explain the reason.
6. Results Table 3: What is the significance of including IgG and IgM for comparison? Please
explain the reason.
7. Results Table 4: The inner diameter of the portal vein in the normal control group is 14mm?
It seems too large. Please explain the reason.
8. Results Table 5: TE threshold 6.46kPa (compared with the citation in the discussion, the
threshold is 19.2kPa)? The threshold of this study is too low. Please explain the reason.
9. Results Table 6: There is a problem with the selection of the cut-off of mild EGV. The AUC
of moderate EGV is low. The cut-off of mild EGV is larger than the moderate. Please explain
the reason.
10. Results Table 6 and Figure 2: The p value of moderate EGV is inconsistent in the chart.
11. Results: The accuracy of other non-invasive indicators in assessing varicose vein
classification was not calculated and should be compared with TE.
12. Results Figure 3: The labeling is unclear. Is it the same patient? What is the degree of varicose
veins in the patient? It is better to mark the varicose veins.
13. Discussion: It is recommended to add the disadvantages of this study.
14. Discussion: The discussion is not in-depth enough and is repeated with the introduction. The
advantages and disadvantages of TE in assessing varicose veins, the comparative discussion of
TE and other diagnostic/grading methods, and whether there are differences in varicose veins
in patients with cirrhosis of different etiologies should be added.
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: 3 Date: 20 Mar 2025
Reviewer's report:
I enjoyed reading this paper on patients' experiences with EO CRC. Very interesting topic, and
the paper reads well.
I have no comments, and I think the paper can be published as is.
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: 3 Date: 25 Mar 2025
Reviewer's report:
Weaknesses and Limitations
Sample and Generalizability:
Small sample size (n=47) limits statistical power and representativeness. Recruitment via patient
organizations may introduce selection bias (e.g., overrepresentation of educated, advocacy-
aware participants).
Methodological Gaps:
Lack of standardized protocols for focus groups (e.g., mixed languages, varying facilitators)
risks inconsistent data collection.
Absence of inter-coder reliability measures in thematic analysis raises questions about
interpretive rigor.
Ethical Oversight Concerns:
While NHS REC approval was not required in the UK, the manuscript does not clarify
compliance with ethics regulations in other EU countries (e.g., Ireland’s HSE framework).
Reliance on internal board approval may not meet all national standards for human-subject
research.
Funding and Conflicts of Interest:
Funding from pharmaceutical companies (Bayer, BMS, Daiichi Sankyo) is disclosed, but the
lack of competing interests statement warrants caution. Industry involvement, even indirect,
could influence study framing (e.g., emphasis on biomarkers/testing).
Data Limitations:
Qualitative focus restricts quantitative analysis of prevalence (e.g., diagnostic delay duration,
biomarker testing rates).
References to future publications (e.g., 2024–2025 studies) as supporting evidence weaken the
literature review’s credibility.
Recommendations for Improvement
Expand Sample Diversity:
Include participants from underrepresented demographics (e.g., lower education levels, rural
areas) to enhance generalizability.
Strengthen Methodology:
Standardize focus group protocols (e.g., uniform language, facilitator training) and employ
mixed-methods approaches for triangulation.
Report inter-coder reliability and reflexivity in thematic analysis.
Address Ethical Gaps:
Clarify compliance with ethics frameworks in all participating countries (e.g., Ireland’s HSE
requirements, EU GDPR for health data).
Deepen Implementation Strategies:
Provide concrete steps for proposed interventions (e.g., how to integrate gender-sensitive
training into medical curricula).
Explore cost-benefit analyses for lowering screening ages, a key policy recommendation.
Mitigate Funding Bias:
Include explicit safeguards in future studies to ensure industry sponsors do not influence research
design or outcomes.