JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 5 Date: 27 Jun 2024
Reviewer's report:
Since the last version , the manuscript seems to be properly corrected according to the reviewers'
suggestions,  so I reccommend its publication in BMC Gastroenterology journal.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 5 Date: 04 Jul 2024
Reviewer's report:
Thank you for your efforts to optimise the manuscript.
I still do have some issues with the responses, especially regarding the Bonferonni corrections
that should be conducted in this kind of research.
Furthermore, there still does not seems to be a clear hypothesis. and some questions are not
sufficiently answered (the type of hospital should be in the manscript for a better understanding
as this is a hospital where ICU beds are scarce, for example, and the 5 missing microbiological
samples are not explained)
In this current state, I do not recommend these data to be internationally published.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 5 Date: 04 Jul 2024
Reviewer's report:
This article has discussed an important and severe disease with potential for fatal complication. I
will generate interest for further study in this field. I will recommend  this article to be published.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 7 Date: 16 Jul 2024
Reviewer's report:
With the revised version I hope article gets accepted. This is an important topic and publication
will attract other readers as well to conduct further study on this topic.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 7 Date: 23 Jul 2024
Reviewer's report:
Same conclusion: In conclusion, some variables might, after correction, be statistically
significantly associated with ICU admission and shock, but whether this association is relevant
remains un-known (e.g., OR 1.04 (1.02-1.07) for PCT).
Some corrections have been made, but the language quality is rather poor. E.g.: “in a teritary
care hospital with a 20 beds in ICU”
In Abstract, methods
- “We investigated patients” : the authors did not investigate patients. It was a retrospective
study. They analysed data from patients that were…
- it still says caused by klebsiella infection. The word infection is still redundant.
Table 1: reference values are still missing.
Table 3: sentence is still incomplete / non-English. Decimals of percentages are still used
inappro-priately.
Table 4, 5 und 6. inadequate use of decimals (for both variables and p values). Table 4 is
there-fore hardly readable. In these tables, Bonferroni corrections are needed according to my
knowledge of statistics. The authors are conducting multiple statistical tests simultaneously.
Each test increases the risk of Type I error, and the correction helps control the overall error
rate. You state in the abstract: “we sought to identify factors associated with..” this is exactly
why you need to do this correction.
“P value” is not written uniformly.
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 7 Date: 27 Jul 2024
Reviewer:  Ehab Elmongui
Reviewer's report:
Dear Authors,
Thank you for your insightful study on prognostic risk factors for pyogenic liver abscess caused
by K. pneumoniae. To ensure the methodological quality and clarity of your research, and
to justify the choice of logistic regression over other potential methods, it is crucial that the
following points are addressed thoroughly:
Flow Diagram Clarification:
• The flow diagram should clearly indicate the total number of patients admitted to the hospital
during the study period and the number of patients who met the diagnostic criteria for pyogenic
liver abscess (PLA) caused by K. pneumoniae.
• Additionally, the flow diagram should detail the number of patients who developed each of
the studied outcomes, especially if all outcomes are listed as primary outcomes.
Justification of logistic Regression Analysis:
Although I found no mistakes in the statistical analysis, the choice of logistic regression over
survival analysis in this prognostic study requires robust justification. Specifically, please
address the following points:
• Is the time to event (such as positive blood culture, septic shock, ICU admission after diagnosis)
not relevant in this context?
• Was there no loss to follow-up among the patients?
• The duration of follow-up for patients diagnosed with PLA caused by K. pneumoniae is not
mentioned. Was the follow-up period sufficient to capture all relevant outcomes?
Presentation of Results:
• There is no need to mention the estimates of non-significant factors in the text, as they are
already included in the tables. Instead, focus on presenting the significant factors along with
their 95% confidence intervals and p-values in both the results section and the abstract.
• Make the rounding of estimates to two decimals only while those of p values to three decimals.
Ehab Elmongui
Biostatistician
Review for 10.1186/s12876-024-03391-9 (2024)

Title: Prognostic Risk Factors for Pyogenic Liver Abscess Caused by Klebsiella pneumoniae
Version: 8 Date: 02 Aug 2024
Reviewer:  Ehab Elmongui
Reviewer's report:
Dear authors,
Thanks for revising the flow diagram.
It is clear for me now why you chose logistic regression analyses but you need to add this in the
methods: all outcomes were assessed within 24 hours of PLA diagnosis.
I  recommend your manuscript to be accepted for publication after the minor revision I
mentioned. I have no other comments
Review for 10.1186/s12876-024-03382-w (2024)

Title: Evaluation of pembrolizumab plus cisplatin and fluorouracil in radical treatment for
patients with T4b esophageal squamous cell carcinoma
Version: 1 Date: 13 Nov 2023
Reviewer's report:
The efficacy of Pembrolizumab + cisplatin + 5-FU for unresectable advanced esophageal cancer
has already been demonstrated in the KEYNOTE-590 trial. This paper is not well up to the
standard of BMC Gastroenterology, this paper should not be acceptable for the publication.
The definition of T4b is not explained in detail. Is it based on the TNM classification or Japanese
classification of Esophageal Cancer ?
Review for 10.1186/s12876-024-03382-w (2024)

Title: Evaluation of pembrolizumab plus cisplatin and fluorouracil in radical treatment for
patients with T4b esophageal squamous cell carcinoma
Version: 1 Date: 27 Nov 2023
Reviewer's report:
-"Efficacy for the primary lesion was evaluated by our original formula for the tumor reduction
rate."  How was this developed and validated?
-Why are these considered induction cases?  A better title might be 'Treatment of T4b ESCC
with pembrolizumab plus cisplatin and 5-fluorouracil ."
-Induction is not indicated for patients that have M1 disease (5 have this).
-You could also include the number of cycles received in the  table 2.
-I think you are making 2 points with this:  1) chemo/pembro better tolerated the DCFJ and 2)
chemo/pembro can be effective.
-There are too few cases to comment on the impact of cps score.
-Fig 1 and discussion of hyperprogression belongs in the results section.
Review for 10.1186/s12876-024-03382-w (2024)

Title: Evaluation of pembrolizumab plus cisplatin and fluorouracil in radical treatment for
patients with T4b esophageal squamous cell carcinoma
Version: 2 Date: 11 Mar 2024
Reviewer's report:
Thank you for correcting some of the previous points, I think the article has improved, though
I still find some limitations to be published in BMC Gastroenterology in its current design:
1) I strongly believe the title should not include "INDUCTION" as it was not the aim of the
KEYNOTE-590 trial to convert patients onto resectable disease or candidates for CHTRTP.
2) In the RESULTS, I continu to find difficult to follow the presentation of the findings,
even if this is a small cohort of patients. Please, consider some of the previous modifications
recommended, separating responders versus non-responders characteristics and adding more
detailed information about the cases. Obviously they had different evolutions and treatments, but
in its current form we lack insights on the value of CHT+ICI to achieve shrinkage of the tumor.
Otherwise, reconsider submitting a new version when more cases and more accurate information
if gathered in the near future
3)  In the DISCUSSION, even if authors submit an article a few months before the review is
performed, I think authors should consider incorporating the suggestions regarding the most
recent update information of the pivotal trial. This is part of the article review process, in which
dilated timelines sometimes imply that authors may rewrite some parts according to newes
data...hence, I think the discussion still lacks strong input comparing the 5-year outcomes of
the KEYNOTE-590 presented in ASCO GI 2024 meeting to put in context de relevance of this
intended submission.
Review for 10.1186/s12876-024-03382-w (2024)

Title: Evaluation of pembrolizumab plus cisplatin and fluorouracil in radical treatment for
patients with T4b esophageal squamous cell carcinoma
Version: 5 Date: 19 Apr 2024
Reviewer's report:
Despite clarifying some points, the article lacks more deepenig into the characteristics of the
patients treated, hence my suggestion would be re-submit with a higher number of patients and
with more detailed information of the cases.
Review for 10.1186/s12876-024-03382-w (2024)

Title: Evaluation of pembrolizumab plus cisplatin and fluorouracil in radical treatment for
patients with T4b esophageal squamous cell carcinoma
Version: 5 Date: 26 Jul 2024
Reviewer's report:
1. Although the number of patients is small, the authors do indicate this is the first ICI/chemo
combined study for induction in ESCC - unique.
2. The study is straightforward and simple. However, they do not include survival or disease free
survival data, This would be useful for the manuscript, particularly as this is a Phase II study.
3. Although the authors state their reasoning, it would still be useful to include RECIST
calculations as it remains a standard.
4. Authors  should discuss latest findings from ASCO with FLOT chemotherapy and how it
compares to their regimen.
5. Please indicate funding source and any trial registration site.
Review for 10.1186/s12876-024-03319-3 (2024)

Title: Primary biliary cholangitis has causal effects on systemic rheumatic diseases: A
Mendelian randomization study
Version: 2 Date: 11 Jun 2024
Reviewer's report:
In this study, the authors aimed to valuate the causal effects of primary biliary cholangitis (PBC)
on systemic rheumatic diseases (SRDs) through Mendelian randomization (MR).
They used the genome-wide association study (GWAS) summary data obtained from MRC IEU
OpenGWAS and FinnGen databases. Independent genetic variants for PBC were selected as
instrumental variables. Inverse variance weighted was used as the main approach to evaluate the
causal effects of PBC on the following SRDs: Sjögren syndrome (SS), rheumatoid arthritis (RA),
systemic lupus erythematosus (SLE), systemic sclerosis (SSc), mixed connective tissue disease
(MCTD) and polymyositis (PM). Horizontal pleiotropy and heterogeneity were measured by
MR#Egger intercept test and Cochran's Q value, respectively. The MR results demonstrated a
positive causal effects of PBC on SRDs, indicating casual effects on various SRDs.
This study is of interest and of clinical significance. However, the following points should
be addressed to further improve the clinical impact: 1) As reported, all PBC cases fulfilled
the American Association for the Study of Liver Disease criteria for PBC. However, SRDs
diagnostic criteria are not reported, but only ICD codes. The authors should reported the
diagnostic criteria of SS, RA, SLE, SSc, MCTD, and PM; 2)  Discussion: to further support the
study results, the authors should recall important previous literature data supporting the concept
that PBC represents on overlap condition between autoimmune hepatology and rheumatology
since PBC patients are characterized by serum positivity of autoantibodies classically detected
in rheumatological patients such as SS-A/Ro-52kD and centromere as previously demonstrated
(Aliment Pharmacol Ther. 2007 Sep 15;26(6):831-8. doi: 10.1111/j.1365-2036.2007.03433.x. )
and the so-called PBC-specific antinuclea r antibodies such as ANA exhibiting the Multiple
Nuclear Dots (MND) or the Rim-Like immunofluorescence patters are detected in SLE, SSc
and SjS, as previously demonstrated (Alimentary Pharmacology and Therapeutics 2006;24
(11-12):1575 - 1583; DOI 10.1111/j.1365-2036.2006.03172.x). Importantly, autoantibodies
directed against nuclear body component such as sp140 protein, have been indentified in
PBC patients , as previously demonstrated (Am J Gastroenterol. 2010 Jan;105(1):125-31. doi:
10.1038/ajg.2009.596.) and may have a pathogenetic significance on both rheumatological
patients and PBC patients, thus supporting the immunological link between rheumatological
disorders and PBC.
Review for 10.1186/s12876-024-03319-3 (2024)

Title: Primary biliary cholangitis has causal effects on systemic rheumatic diseases: A
Mendelian randomization study
Version: 2 Date: 18 Jun 2024
Reviewer:  Cristiana Sieiro Santos
Reviewer's report:
The manuscript evaluates the causal effects of PBC on SRDs through Mendelian randomization
(MR).
The introduction provides a clear overview of PBC, highlighting its autoimmune nature,
prevalence, and the need for better therapeutic strategies. It effectively sets up the rationale for
investigating the link between PBC and SRDs.
- Please change: "Characterized by destoryed interlobular bile ducts" should be corrected
to "characterized by destroyed interlobular bile ducts."; "an increased requirement for liver
transplantation" could be rephrased for clarity to "an increased need for liver transplantation."
and "PBC is female-predominant, and the prevalence of PBC is on the rise" is redundant. It could
be simplified to "PBC is predominantly found in females, and its prevalence is increasing."
- The introduction should emphasize the significance of using MR to establish causality in
epidemiological research: "Using genetic variation as instrumental variables in MR analysis
helps evaluate the causal effects of exposures on outcomes, potentially reducing the impact of
confounding factors."
The methods:
The section could benefit from a brief description of how genetic variants are chosen as
instrumental variables (IVs) for readers unfamiliar with MR analysis.
Discussion:
- Typographical Errors: Correct minor typos, such as "destoryed" to "destroyed" and "unsolved"
to "unresolved."
- Ensure consistent use of abbreviations, e.g., "SRDs" for systemic rheumatic diseases.
- Improve sentence clarity. For example, "Our research aimed to evaluate the causal effect of
PBC on SRDs, a matter that was unresolved in previous observational epidemiological studies."
- Highlight more prominently how the study’s findings align or contrast with previous
observational studies. For example, "Previous studies have reported associations between PBC
and SRDs, but our MR analysis provides stronger evidence for a causal relationship."
- Expand on the potential mechanisms linking PBC and SRDs. For instance, "The liver, as
a major lymphoid organ, plays a crucial role in immune responses, which may explain the
observed associations."
-  Provide a deeper discussion of immune mechanisms, such as the role of Th1/Th17 cells and
specific cytokines in PBC and SRDs.
- Discuss the shared genetic pathways, such as IL12-mediated signaling involving STAT4 and
IRF5, in more detail.
- Address the limitations related to the study population. "Our MR analysis was conducted in
a European population, and the findings may not generalize to other ethnic groups. Gender-
specific effects were also not explored due to data limitations."
- Mention the limitation of analyzing only six SRDs. "While our study focused on six SRDs,
other autoimmune conditions might also be associated with PBC."
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 2 Date: 29 Oct 2023
Reviewer's report:
This study was conducted retrospectively to identify risk factors for BHS following PD surgery.
The topic was clinically interesting. The paper was well-structured and the hypotheses were
tested appropriately. The interpretation of the results was also clear and valid.
I request clarification from the authors on some minor issues.
1. Hazard ratio (HR) seems more appropriate than Odds ratio (OR) for analyzing data collected
in retrospective studies.
2. There are grammatically inappropriate expressions: The median incidence of BHS was 395
days (172-696) after PD (Table 4). Wouldn't it be more appropriate? For example, the median
time to occurrence of BHS.
3. Based on the research results, what efforts are needed to prevent or reduce the occurrence of
BHS? Describe the clinical and applied significance of the results.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 2 Date: 29 Oct 2023
Reviewer's report:
Reviewer comments to author
This paper described about benign hepaticojejunostomy strictures after
pancreatoduodenectomy. This well-written manuscript is mildly interesting that male and non-
dilated bile duct are risk for postoperative anastomotic stricture; however, these are known
factors and luck of novelty. Moreover, this study is a retrospective study from single center,
therefore, it’s still uncertain whether these factors could be risk factors for anastomotic stricture.
Some of the other major limitations include:
Major revision
# You described that preoperative bile duct diameter of 8.8 mm or less was risk factor for
anastomotic stricture. How many patients with this criteria suffered from anastomotic stricture?
# In the patients with small bile duct, what is the risk factor for anastomotic stricture? For
example, patients with non bile duct cancer?
# In BHS group, only one patient had bile duct cancer. Please describe the detail of this patient.
Is this patient had preoperative small bile duct?
I hope these comments will be helpful.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 4 Date: 02 Feb 2024
Reviewer's report:
Thank you for making changes to your paper after our feedback. Your paper is now much better
than before. However, there are still some small things that need your attention. I believe fixing
these will make your paper even better.
I am excited to see how your research will grow and how it will help in medical fields in the
future.
Detailed comments:
About your findings on patients with a bile duct size of 8.8mm or less, it seems no specific
factors causing BHS were found. It's important to look into problems for patients with small bile
ducts. Even if there wasn't a clear statistical difference, did you notice any patterns? Could you
add a table that shows the difference between patients with BHS and those without, focusing on
those with small bile ducts? Please use the same factors you listed in Table 2 for this comparison.
I hope these suggestions help make your paper even better.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 4 Date: 04 Feb 2024
Reviewer's report:
1. In the Methods: according to a request provided by one of the previous reviewers, the authors
have provided a detailed description of the postoperative follow-up employed. However, I
feel that the most important point is still missing here. When do they establish that a biliary
anastomotic stricture is present? Is it always and only a radiologic definition? In this case,
did they employ a given diameter threshold to define the stenosis? This is pivotal for the
reproducibility of the study results.
2. In the Methods: a definition of preoperative and routine, early postoperative biliary duct
measurement is provided in the paragraph dedicated to biliary anastomosis stricture definition.
The authors are invited to move the last sentences of the paragraph accordingly.
3. In the Methods: ‘filamentous bile duct stenosis’ is inappropriate wording.  I would suggest
removing the adjective.
4. In the Methods and Figures: why were continuous variables described as mean only? I would
suggest using the median instead. In the figures, it should be specified whether means or medians
are reported.
5. In the Results: compared to the original submission, the authors have included a sentence
regarding a case in which a biliary anastomotic stricture occurred in a patient with bile cancer.
They reported an ‘improvement’ in the bile duct measurement from preop to postop. Why did
they do that? What is the sense of this detail?
6. In the Results, Multivariate analysis: formally speaking, this is a multivariable analysis.
Furthermore, they added the sentence: BHS occurred in 13 (7.4%) of the 175 cases reviewed,
11 (84.6%) of the 13 cases had a bile duct diameter of 8.8 mm or less, and 10 (76.9%) were
male. It seems inappropriate to present these data here. Instead, this should be incorporated in
the paragraph ‘comparison of the BHS and non-BHS groups’.
7. In the Results: the sentence: In all 13 cases in which the BHS had occurred, 539 days
(365-1959) had elapsed since the last ERC, with no recurrence of BHS. is unclear. What do the
authors mean? I would suggest removing this sentence.
8. In the Discussion: the authors state that postop cholangitis was not included in the
multivariable model. However, it seems to be included according to the revised table 3. Please
clarify.
9. General comment: despite being generally improved from the original submission, scientific
English writing still needs proofreading before publication. There are several occasions in which
writing sounds clumsy and inappropriate to the context. I would suggest having an expert
scientific writer involved who is fond of surgical and anatomical descriptions and data reporting.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 4 Date: 13 Feb 2024
Reviewer's report:
Authors’ responses were appropriate. However, However, I still have doubts about whether
logistic analysis is a more appropriate method than cox regression analysis. Time is also thought
to be an important factor in the development of BHS. To present more accurate results, it seems
necessary to consult a biostatistician, consistent with Reviewer 3's comments.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 5 Date: 02 Aug 2024
Reviewer's report:
Thank you for addressing my queries comprehensively. The response provided sufficient detail
and clarity regarding the comparison of patients with a preoperative bile duct diameter of 8.8
mm or less. The inclusion of additional information in the revised version to further analyze
factors listed in Table 4 is commendable.
I believe this manuscript meets the standards for publication and is suitable for acceptance.
Review for 10.1186/s12876-024-03388-4 (2024)

Title: Benign hepaticojejunostomy strictures after pancreatoduodenectomy
Version: 5 Date: 12 Aug 2024
Reviewer's report:
I read with interest the revised version of the manuscript. I can see that the work has been
significantly improved since the initial submission. I do not have additional comments.
Review for 10.1186/s12876-024-03361-1 (2024)

Title: Meta-analysis of the Effectiveness of Early Endoscopic Treatment of Acute Biliary
Pancreatitis based on Lightweight Deep Learning Model
Version: 1 Date: 03 Mar 2024
Reviewer's report:
Thanks for the opportunity to review the manuscript by Xiong et al. “Meta-analysis of the
Effectiveness of Early Endoscopic Treatment of Acute Biliary Pancreatitis based on Lightweight
Deep Learning Model”. It is a well-written, understandable article with highly innovative
character about a relevant clinical picture. I would recommend the publication of this article in
BMC Gastroenterology.
Xiong and colleagues developed a deep-learning model to justify articles about endoscopic
management of acute biliary pancreatitis. Authors describe a meaningful symbiosis of
information technology and traditional review processes. From over 3200 articles, the authors
were able to select 8 as suitable for their analysis after an extensive analysis process.
Not surprisingly, ERCP was found to be an effective procedure with minimal complications.
However, the method of analysis described in the systematic review and meta-analysis is
sufficiently innovative to recommend that the article be published.
I congratulate the authors on a successful article and have no requests for changes.
Review for 10.1186/s12876-024-03361-1 (2024)

Title: Meta-analysis of the Effectiveness of Early Endoscopic Treatment of Acute Biliary
Pancreatitis based on Lightweight Deep Learning Model
Version: 1 Date: 27 Mar 2024
Reviewer's report:
The authors evaluated the clinical outcomes of early ERCP for ABP comparing with delayed
ERCP. The methods for extracting data and articles were described in great detail. And the
result showed that no remarkable differences were detected in mortality, the incidence of
complications, and operation time between early and delayed groups, while hospitalization
duration in the early group was notably shorter than that in the delayed group.
This is a well written, interesting paper, and useful contributing to clinical practice.
However, I would like to suggest some issues with several comments and criticisms as follows;
Comment 1:
The biggest concern with early ERCP for ABP is exacerbation of pancreatitis. However, the
procedure-related adverse events of ERCP in the both group were not investigated in this
manuscript. The authors needs to clarify this point.
Comment 2:
There are various treatments for therapeutic ERCP for ABP, such as papillary procedure, biliary
drainage, and pancreatic drainage.
The authors needs to explain what procedure is desirable in early ERCP for ABP and provide
supporting literatures.
Comment 3:
Discussion session: Page 22, line 352
“Some recent research show that delayed ERCP increases the incidence of recurrent biliary
events versus early ERCP, such as recurrent pancreatitis, cholecystitis, and biliary colic.” Please
refer to the literatures and add the reason for this.
Comment 4:
Results session: Page 21, line 325
As the author presents, the most common causes of ABP are cholecystolithiasis and bile
duct stones. In daily clinical practice, when the presence of stones is uncertain, EUS is often
performed to omit unnecessary ERCP and result in a favorable clinical course.
In these cases, early ERCP is unnecessary, so this point also needs to be discussed with reference
to the literatures.
Review for 10.1186/s12876-024-03361-1 (2024)

Title: Meta-analysis of the Effectiveness of Early Endoscopic Treatment of Acute Biliary
Pancreatitis based on Lightweight Deep Learning Model
Version: 1 Date: 19 Jun 2024
Reviewer's report:
The timing of ERCP in acute biliary pancreatitis is import in clinical practice. I think this is
well written article with proper study design and analytic method. There are several points to
be clarified and revised.
Major
1. Could you present the comparison of post-ERCP mortality and morbidiy subgroup analysis
according to the severity of acute pancreatitis?
2. How the result “the meta-analysis demonstrated that no remarkable differences were detected
in the incidence of complications, mortality, and operation time between patients undergoing
ERCP in early stage and those receiving delayed ERCP.” supports the conclusion “treatment of
biliary pancreatitis with early ERCP was very safe”
Minor
1. Line 126-127, “foeward” should be corrected to “forward”.
Review for 10.1186/s12876-024-03381-x (2024)

Title: Prognostic value of hemoglobin to red blood cell distribution width ratio in pancreatic
ductal adenocarcinoma: A retrospective study
Version: 1 Date: 23 Jun 2024
Reviewer:  Jörg Kleeff
Reviewer's report:
The current manuscript presents a retrospective single center study on 128 patients with
pancreatic cancer. Various prognostic factors were analysed. It is shown that hemoglobin to red
blood cell distribution width ratio (HRR) was an independent predictor for overall and disease
free survival.
The identification of relevant prognostic markers for pancreatic cancer is an important topic.
There are, however, several concerns that the authors should address:
One major drawback of the present study is the relatively small cohort of 128 patients, and the
single center design. There is no training and validation cohort. Therefore, it is difficult to draw
meaningful conclusions.
Further, there is a lack of clinical implications. What can we do with this information. Do
the authors suggest to stratify patients depending on HRR (e.g. neoadjuvant therapy yes/no, or
prehabilitation, or RBC transfusion)?
It would be important to provide information on the HRR marker, besides its prognostic
relevance in various cancers. What is this ratio actually measuring? How is it related to chronic
blood loss and bone marrow function? The introduction is very short and not very informative
The cut-off value of HRR was set at 0.88. First, it is not clear how this was established (what
does it mean ‘based on the ROC cut-off value’?). Second, is this the best cut-off value? There
might be better values to identify patients with worse prognosis.
The authors could have also checked whether a combination of markers (e.g. CA19-9 plus HRR
plus other markers) would be superior to each marker alone.
Review for 10.1186/s12876-024-03381-x (2024)

Title: Prognostic value of hemoglobin to red blood cell distribution width ratio in pancreatic
ductal adenocarcinoma: A retrospective study
Version: 2 Date: 14 Jul 2024
Reviewer:  Jörg Kleeff
Reviewer's report:
Although some general and specific concerns remain, the authors have satisfactorily answered
most of the questions and concerns of the reviewer. I believe that this is an interesting manuscript
that has been strengthened by the additions and changes.
Review for 10.1186/s12876-024-03383-9 (2024)

Title: Genetic Associations of Birthweight, Childhood, and Adult BMI with
Metabolic Dysfunction-associated Steatotic liver disease: A Mendelian Randomization
Version: 1 Date: 20 May 2024
Reviewer:  Panagiotis Tsibouris
Reviewer's report:
The study uses SNP data to evaluate any connection of NAFLD with birth and childhood weight
The idea is innovative  The abstract should make clear this innovation as well as diagnosis of
NALFLD As far as metabolic data are available the new diagnosis of MASLD could be used
instead. The authors should define the diagnosis of NAFLD or MASLD Their is a hint that a
national database was used but still criteria of NAFLD should be defined Was the diagnosis
based on liver biopsy, MRI, US or any algorithmic diagnosis The difference is important Also
data on birth and childhood weight should be defined if they are based on a database or if they
represent a certain retrospective recording At what age childhood weight has been recorded
and what was normal  The authors should give a hint about their data not being coherent with
previous bibliography suggesting a relation of birth weight high or low to   NAFLD development
Are there any data about blood sugar or insulin available?
Review for 10.1186/s12876-024-03383-9 (2024)

Title: Genetic Associations of Birthweight, Childhood, and Adult BMI with
Metabolic Dysfunction-associated Steatotic liver disease: A Mendelian Randomization
Version: 1 Date: 16 Jun 2024
Reviewer:  Tarana Gupta
Reviewer's report:
Authors have done a meticulous analysis of available database for finding association of
birthweight, adult and childhood BMI with NAFLD.  I have few comments and suggestions.
1. They have taken all data for European population. The strength of the study is uniformity for
this association minimising bias due to geographical regions.  On the contrary, findings of the
study can not be generalised.
2. There is extensive statistical analysis, therefore, reviewers should include statistician to check
for robustness of methods.
Review for 10.1186/s12876-024-03383-9 (2024)

Title: Genetic Associations of Birthweight, Childhood, and Adult BMI with
Metabolic Dysfunction-associated Steatotic liver disease: A Mendelian Randomization
Version: 4 Date: 22 Jul 2024
Reviewer:  Panagiotis Tsibouris
Reviewer's report:
The authors have successfuly addressed all questions posed in previous review I donot know if
it would be relevant since data from SNPs are available to enter those data in the text
Review for 10.1186/s12876-024-03374-w (2024)

Title: A Novel Nomogram Based on inflammatory-nutritional Biomarkers For Gallbladder
Cancer after Surgical Resection
Version: 1 Date: 26 Jun 2024
Reviewer:  Anwar Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below:
- Have follow-up assessments been conducted to track the progress or changes in the patients'
condition over time?
- Can you perform a comprehensive analysis of the specific indicators to gain a deeper
understanding of the data and its implications?
- Was a forest plot created to visually display the independent predictors of poor prognosis and
validate the model's accuracy?
- What were the overall survival and recurrence rates observed in the study?
- Have clinical characteristic parameters, such as tumor margins, invasion, and metastasis, been
thoroughly evaluated to provide a comprehensive understanding of the clinical profile of the
patients?
Review for 10.1186/s12876-024-03374-w (2024)

Title: A Novel Nomogram Based on inflammatory-nutritional Biomarkers For Gallbladder
Cancer after Surgical Resection
Version: 1 Date: 02 Jul 2024
Reviewer's report:
The development of predictive nomograms for overall survival in cancer research is of
paramount clinical significance. These tools empower clinicians to make informed decisions and
enhance patient outcomes. Basing the nomogram on inflammatory biomarkers is a thoughtful
and clinically relevant approach .The presentation of the results and methodology in this paper
is commendable. The clarity and organization make it easy for readers to follow the research
process. Well done!
I have few comments:
Was the proportional hazards assumption met for all the final predictors? Please add the results
of the Schoenfeld residuals analysis in the supplementary materials.
Provide more details on how the linear predictor values were converted to the simplified risk
scores (points).
Review for 10.1186/s12876-024-03374-w (2024)

Title: A Novel Nomogram Based on inflammatory-nutritional Biomarkers For Gallbladder
Cancer after Surgical Resection
Version: 2 Date: 16 Jul 2024
Reviewer's report:
Thank you for your diligent and thorough revisions to the manuscript titled "[ A Novel
Nomogram Based on inflammatory-nutritional Biomarkers For Gallbladder Cancer after
Surgical Resection]." I appreciate the effort and attention to detail you have demonstrated in
addressing the concerns and suggestions I previously raised.
The inclusion of the Schoenfeld residuals analysis results in the supplementary materials has
significantly strengthened the robustness of the findings. Additionally, the detailed explanation
on how the linear predictor values were converted to the simplified risk scores (points) has
enhanced the clarity and comprehensibility of the methodology.
The revised manuscript now provides a comprehensive and well-substantiated predictive
nomogram for overall survival based on inflammatory biomarkers, maintaining the high
standards of clarity and organization that I initially commended.
I am pleased to inform you that I recommend accepting this manuscript for publication.
Congratulations on this valuable contribution to cancer research.
Review for 10.1186/s12876-024-03374-w (2024)

Title: A Novel Nomogram Based on inflammatory-nutritional Biomarkers For Gallbladder
Cancer after Surgical Resection
Version: 2 Date: 17 Jul 2024
Reviewer's report:
The overall survival rate of patients with GBC is typically poor, with less than 10% surviving
beyond five years. I think this is a very meaningful study. But there are some minor issues.
1. I think clinical articles need a process diagram details the selection of the included patients.
2. Can Table 1 and Table 2 have too much duplicate information merged into one table.
3. Does this study have an external validation set of data to verify the accuracy of the model
Review for 10.1186/s12876-024-03369-7 (2024)

Title: A dynamic model to predict early occurrence of acute kidney injury in ICU hospitalized
cirrhotic patients: A MIMIC database analysis
Version: 3 Date: 23 Jun 2024
Reviewer's report:
The author reports that they developed and validated a dynamic online nomogram which can
be an easy-to-use tool for predicting the individualized risk of AKI in critically ill patients with
cirrhosis. It is interesting; however, I had a few questions about this study.
1. For AKI study, how to definite the baseline serum creatinine is important and should be
provided.
2. It is better to provide how many patients whose variables >20% missing values were excluded.
3. In the manuscript, the author showed that the final logistic model incorporated five
independent predictors (MAP, UV, WBC, TB, and GCS) and was developed as a simple-to-
use nomogram.
(1) As SOFA score includes the GCS score, I am confused why did the author select both these
two score as two potential risk factors?
(2) Urine volume per se is one of the diagnosis criteria for AKI, it seems not suitable be a
potential risk factor for AKI.
4. Since different kinds of antibiotics have different renal toxicity, the author should provide
more detail about the use of antibiotic.
5. As we know, chronic hypertension can also impair renal function, but the Table 1 showed that
patients without AKI had a higher proportion of hypertension [190 (37.3%) vs. 243 (31.4%),
P=0.029].Can the author explain why?
Review for 10.1186/s12876-024-03369-7 (2024)

Title: A dynamic model to predict early occurrence of acute kidney injury in ICU hospitalized
cirrhotic patients: A MIMIC database analysis
Version: 4 Date: 16 Jul 2024
Reviewer's report:
Objective:
The authors develop a predictive model of short-term AKI (<7 days) in cirrhotic patients
hospitalized in intensive care based on the MIMIC database.
General Impression:
The manuscript has precisely addressed the comments of the reviewers from the previous round,
and I congratulate the authors for considering them, significantly improving the quality of the
manuscript.
Major Points:
a. There is no mention in the manuscript of the causes of AKI retained, particularly hepatorenal
syndrome, a specific form of AKI in cirrhotic patients with a prognosis and therapy very different
from other causes of AKI. (DOI: https://doi.org/10.1016/j.jhep.2024.03.031). I would encourage
the authors to propose an annexed table listing the causes of AKI retained for diagnosis.
Minor Points:
I have notified some minor typographical and grammatical errors
• 46 : Acute kidney injury (AKI) is defined as a significant acute reduction in renal function and
is one of the most common complications in critically ill patients with cirrhosis, especially in
the intensive care unit (ICU)
• 57/59 : Therefore, early identification of ICU patients with cirrhosis who are at a high risk of
AKI is very important and may be helpful in providing timely medical interventions to improve
the prognosis of these patients.
• 103/04 : If there were multiple stays in the ICU during hospitalization, the data from the first
admission to the ICU was used
• 124/125 : liver transplantation before admission or during the hospital stay.
• 128 : m2) >90 days (19).
Review for 10.1186/s12876-024-03377-7 (2024)

Title: Predictive factors of portal hypertensive enteropathy exacerbations based on long-term
outcomes
Version: 0 Date: 02 Jul 2024
Reviewer's report:
The paper aimed to clarify the clinical significance and predictive factors of capsule endoscopic
findings of PHE based on long-term outcomes. The study is of high practical value and the
content of the paper is rich. It is suggested to make the following modifications:
1.Further optimize the image content, as some images have low image clarity.
2.It is recommended to appropriately increase the proportion of high-quality papers from recent
years in the reference section.
3.It is advisable to further clarify the logical relationships in the discussion section.
Review for 10.1186/s12876-024-03377-7 (2024)

Title: Predictive factors of portal hypertensive enteropathy exacerbations based on long-term
outcomes
Version: 0 Date: 06 Jul 2024
Reviewer's report:
The study offers valuable insights into the clinical significance and predictive factors of Portal
hypertensive enteropathy (PHE) exacerbation, which could contribute to better management of
PHE. However, several issues need further clarification:
With the exacerbated group consisting of only 19 patients, including more than two predictors
in the model could lead to overfitting and inflation of the results.
Potential information bias in the study could compromise the reliability of the findings.
The study might not fully account for confounding variables such as differences in
comorbidities, varying degrees of adherence to treatment, or differences in treatment regimens.
Review for 10.1186/s12876-024-03365-x (2024)

Title: Effect of Different Working Periods on Missed Diagnosis of Colorectal Polyps in
Colonoscopy
Version: 1 Date: 18 Jun 2024
Reviewer's report:
In their work, the authors study an important issue related to endoscopy services and more
importantly to patient management. The issue of endoscopist fatigue or lack of time can have a
significant impact on the diagnosis and treatment of patients with colorectal polyps or cancers.
However, prior to further consideration of acceptance for publication I suggest major revisions
with language and grammar check. Furthermore, I have the following comments:
1. Throughout the abstract the outcome is reported as ”miss rate of patients”. This is a bit
misleading, as I believe the authors are looking at “missed diagnosis of colorectal polyps” as
stated in the title. The definition in the methods section of the manuscript does explain this, but
when reading the abstract this is not presented. I still recommend changing the phrasing to miss
rate of polyps / diagnosis in stead of miss rate of patients.
2. The authors state that The different working periods had no significant effect on the miss
rate of patients #P=0.849) (page 1, line 14-15) and The number of missed polyps was not
significantly affected by different working periods (P=0.849). (page 6, line 7-8).  I recommend
specifying whether this is referring to statistical or clinical significance.
3. In the methods section I would recommend describing that patients with no polyp findings
in the first colonoscopy are not analyzed in this study. This is only mentioned in the discussion
as a limitation to the study.
4. The following paragraph is a bit unclear: The analysis of different weeks of colonoscopy,
doctor's gender, whether performance assessment, whether same endoscopist or same
department, and the size of the largest polyp also did not significantly affect the miss rate of
patients. (page 5, line 15-18).
I would suggest to clarify the meaning of performance assessment and to specify that whether
same endoscopist or same department refer to the first and second colonoscopy being performed
by the same endoscopist or in the same department. I cannot find comparisons on doctors gender
in table one, and I need an argument for why the gender of the endoscopist should be considered
in this regard. I suggest removing this.
5. Throughout the manuscript, the authors report some results as only p-values. I would
recommend to report the point estimate as well or omit the p-value in the text, as it is difficult
for the reader to evaluate whether the result is clinically significant based only on the p-value.
Review for 10.1186/s12876-024-03365-x (2024)

Title: Effect of Different Working Periods on Missed Diagnosis of Colorectal Polyps in
Colonoscopy
Version: 1 Date: 18 Jun 2024
Reviewer's report:
This manuscript is useful for adding to the body of relevant literature. However, several issues,
among them language and grammar issues, need to be sorted before publishing. Another issue is
the definition of experience-expertise of endoscopists/colonoscopists (which, based on the time
spent in endoscopy, is rather 'fluffy' and has to be clearly defined.
Review for 10.1186/s12876-024-03365-x (2024)

Title: Effect of Different Working Periods on Missed Diagnosis of Colorectal Polyps in
Colonoscopy
Version: 2 Date: 15 Jul 2024
Reviewer's report:
The manuscript has improved significantly.
I only have  a few comments.
Overall I appreciate the willingness to include some point estimates. In my comments I was
aiming at the proportions, such as you report regarding  the experience level of the endoscopists,
and not as much the Chi2 or fishers exact test results. My request was for those instances where
it makes sense in the text.
1.  Page 3, line 3: colonoscopies is misspelled.
2. On page 3, line 6-7 you the authors state: "...aged 26–28 years, with an average age of (57.76
± 11.33) years". I would believe that the age of 26-28 is a mistake as this does not match the
average age.
3. page 3, line 13: gastroscopy is misspelled.
4. Page 6, line 18-19: I would suggest rephrasing: "There was no statistically significant effect
on the number of missed polyps by different working periods "
Review for 10.1186/s12876-024-03356-y (2024)

Title: Efficacy of probiotics, prebiotics, and synbiotics on liver enzymes, lipid profiles, and
inflammation in patients with non-alcoholic fatty liver disease: a systematic review and meta-
analysis of randomized controlled trials
Version: 2 Date: 18 Nov 2023
Reviewer's report:
All comments addressed completely.