JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03161-7 (2024)

Title: The impact of Karnofsky Performance Status on prognosis of patients with hepatocellular
carcinoma in liver transplantation
Version: 1 Date: 09 Jul 2023
Reviewer's report:
This is a simple paper using the KPS score to stratify different groups of LT patients, but focusing
on the HCC status and recurrence of the disease after LT.
What is not clear in this paper is the role of low KPS and how not influences the poorer
performance in terms of liver transplantation? It boils down to selection of patients for LT and
would there be any data regarding prehabilitation for these low KPS score patients to make them
fitter before LT?
What would be the postulation of the authors on the poorer survival of low KPS score patients
with LT for HCC with higher recurrence? Any we suggesting that low KPS is associated with
more aggressive cancer? I will find this difficult to provide concrete evidence. However, the
authors should try to address that as this is one of the. main findings in the paper.
Review for 10.1186/s12876-024-03161-7 (2024)

Title: The impact of Karnofsky Performance Status on prognosis of patients with hepatocellular
carcinoma in liver transplantation
Version: 1 Date: 12 Aug 2023
Reviewer:  Deok Gie Kim
Reviewer's report:
The authors tried to investigate the association between pre-transplant KPS score and long-term
outcomes in HCC patients listed for liver transplantation. Association between KPS before LT
and waiting list and post-LT mortality have been well-explored whereas relation with HCC
outcome has not. The conclusion of authors was negative for HCC recurrence, but positive for
survival, which were not novel finding. However, I think their finding would be informative
enough to be published in the journal if they clarify the purpose of the study.
There are several points needing major revision.
Most important point : what is the main purpose of this study? As the title says, association
between KPS and HCC outcome after LT? Then authors should clarify the primary purpose with
corresponding changes of whole study flow.
#Abstract
1. In the method, primary and secondary end points should be clearly descripted. Primary end
point of this study is HCC recurrence after LT, not ITT survival or OS after LT, wasn’t it? If I’m
true, authors should re-check the direction of the study flow and major point of abstract. If the
association between KPS and HCC recurrence after LT is the key point of this study, I suggest
ITT survival for wait-listed patients should be removed or moved to supplement. In this case,
study population could be changed to including LT recipients only.
2. In the results, please mention 5y ITT survival (if it should be included), post-transplant
survival and HCC recurrence. Also, HR with 95% CI should be presented for the results of Cox
and competing risk regression.
3. Conclusion should be fitted to the main purpose of the study (current form is in line with
the title though)
#Background
Background is too long and redundant. Please reduce it to an half of current form.
#Method
1. Too many abbreviations have been used. Use abbreviations only where essential.
2. “The time-dependent effects of KPS for survival were investigated based on Schoenfeld’s
residuals”  => please reference for this method
#Results
1. Results also should be corrected according to adequate primary and secondary end point and
study inclusion as mentioned above.
2. 1 digits after decimal point would be adequate for presenting survival rates.
3. 2 digits after decimal point would be adequate for presenting HR and 95% CI
4. Table 2 and 3 are two redundant. They should be moved to supplement and make 1 or 2
tables showing multivariable analyses for outcomes only including variables included in the
multivariable models.
5. Survival curves should be presented with number at risk.
6. curve for dropout do not need to be in main results. Please move it to supplement.
7. Please rearrange curves in 1 figure with multiple panels.
8. Legend is missing in the supplement figure 1.
Review for 10.1186/s12876-024-03161-7 (2024)

Title: The impact of Karnofsky Performance Status on prognosis of patients with hepatocellular
carcinoma in liver transplantation
Version: 3 Date: 27 Dec 2023
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Probably - with minor revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: Overall, the revised manuscript is better-structured, with each
section logically flowing into the next. The authors have effectively addressed initial comments.
One aspect that initially eluded my attention is the publication of a Chinese research team
utilizing a U.S. database. It would be beneficial for the authors to provide a more detailed
explanation of how they accessed the data, including clarifications on data ownership and the
permissions obtained for data use.
ADDITIONAL REQUESTS/SUGGESTIONS:
- Tables 2 and 3 are self-explanatory, and thus, there is no need to repeat the information within
the text (it makes it more difficult to follow)."
Review for 10.1186/s12876-024-03161-7 (2024)

Title: The impact of Karnofsky Performance Status on prognosis of patients with hepatocellular
carcinoma in liver transplantation
Version: 4 Date: 15 Jan 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: I’m happy with the latest response from the authors.
I have no further comments.
Review for 10.1186/s12876-024-03160-8 (2024)

Title: Comparative Study of Ultrasound Attenuation Analysis and Controlled Attenuation
Parameter in the Diagnosis and Grading of Liver Steatosis in Non-alcoholic Fatty Liver Disease
Patients
Version: 0 Date: 20 Jan 2024
Reviewer:  Giuseppe Guido Maria Scarlata
Reviewer's report:
The manuscript evaluate the Ultrasound Attenuation Analysis and Controlled Attenuation
Parameter in the diagnosis and grading of NAFLD, showing an high sensitivity and specificity
of USAT. This may improved the diagnostic approach of NAFLD in clinical practice. I suggest
some revision to improve the manuscript:
1. You can discuss this recent paper doi: 10.3390/medicina59111935
2. You should discuss the sensitivity and specificity of CAP and US.
3. I suggest improving the conclusions. They are too concise.
4. Why the waist circumference was not assessed?
Review for 10.1186/s12876-024-03160-8 (2024)

Title: Comparative Study of Ultrasound Attenuation Analysis and Controlled Attenuation
Parameter in the Diagnosis and Grading of Liver Steatosis in Non-alcoholic Fatty Liver Disease
Patients
Version: 0 Date: 21 Jan 2024
Reviewer's report:
In the Method section, please specify the third exclusion criteria for NAFLD participants: use
of fat-preparation.
Error factors that may influence the ultrasound elastography technique, the Controlled
Attenuation Parameter (CAP) used have been excluded? Conditions as: cytolysis, cholestasis,
congestion, amyloidosis, lymphomas, and extramedullary hematopoiesis were not mentioned in
the exclusion criteria, although they may alter the results of the CAP.  Were the patients included
evaluated by CAP outside of episodes of cytolysis or cholestasis?
In the Discussion section discuss more on the accuracy and cutoff values. Compare the cutoff
values of your study with the optimal cutoffs established in meta-analyses for the prediction
of mild (S1), moderate (S2), and severe (S3) steatosis. The cut-off values were established at
248 dB/m, (AUC 0.823, Se 68.8%, Sp 82.2%), 268 dB/m, (AUC 0.865, Se 77.3%, Sp 81.2%),
and 280 dB/m (AUC 0.882, Se 88.2%, Sp 77.6%) for detecting steatosis #S1, #S2, and S3,
respectively.
- Karlas T., Petroff D., Sasso M., Fan J.G., Mi Y.Q., de Lédinghen V., Kumar M., Lupsor-
Platon M., Han K.H., Cardoso A.C., et al. Individual patient data meta-analysis of controlled
attenuation parameter (CAP) technology for assessing steatosis. J. Hepatol. 2017;66:1022–1030.
doi: 10.1016/j.jhep.2016.12.022).
- Lup#or-Platon M, Feier D, Stefanescu H, Tamas A, Botan E, Sparchez Z, Maniu A, Badea R.
Diagnostic accuracy of controlled attenuation parameter measured by transient elastography for
the non-invasive assessment of liver steatosis: a prospective study. J Gastrointestin Liver Dis.
2015; 24:35–42.
It is suggested that these cut-offs should be further adapted for particular settings as they were
influenced by several covariates. Specifically, it was suggested that practitioners should deduct
10 dB/m from the CAP value for NAFLD/NASH patients, deduct 10 dB/m for diabetes patients,
and deduct/add 4.4 dB/m for each unit of BMI above/below 25 kg/m2 over the range of 20–
30 kg/m2.
- Taru MG, Neamti L, Taru V, Procopciuc LM, Procopet B, Lupsor-Platon M. How to
Identify Advanced Fibrosis in Adult Patients with Non-Alcoholic Fatty Liver Disease (NAFLD)
and Non-Alcoholic Steatohepatitis (NASH) Using Ultrasound Elastography-A Review of the
Literature and Proposed Multistep Approach. Diagnostics (Basel). 2023 Feb 19;13(4):788. doi:
10.3390/diagnostics13040788. PMID: 36832276; PMCID: PMC9955630.
-  Petroff D, Blank V, Newsome PN, et al. Assessment of hepatic steatosis by controlled
attenuation parameter using the M and XL probes: an individual patient data meta-analysis.
Lancet Gastroenterol Hepatol. 2021; 6:185–198.
Your references should be updated.
Review for 10.1186/s12876-024-03156-4 (2024)

Title: Reading of Small Bowel Capsule Endoscopy After Frame Reduction Using an Artificial
Intelligence Algorithm
Version: 2 Date: 01 Sep 2023
Reviewer's report:
The authors proposed an artificial intelligence algorithm for frame reduction of Small Bowel
Capsule Endoscopy Images to help doctors complete diagnostic tasks. And experiment showed
that the proposed AI algorithm can remove the image of poor visualization in SBCE and achieve
competitive results compared to AI non-user groups. However, there are some issues that need
to be addressed before publication.
(1) Which AI algorithm did the authors use? And how to train the AI algorithm?
(2) What is the motivation of the study?
(3) In the introduction, please add some recent literature. For example:
[1]. Gong E, Bang C, Lee J, et al.: Deep-learning-based clinical decision support system for
gastric neoplasms in real-time endoscopy: Development and validation study. Endoscopy AAM
2023.
[2]. Tang S, Yu X, Cheang C, et al.: Transformer-based multi-task learning for classification and
segmentation of gastrointestinal tract endoscopic images: Computers in Biology and Medicine
2023 (157): 106723.
[3]. Du H, Dong Z, Wu L, et al.: A deep-learning based system using multi-modal data for
diagnosing gastric neoplasms in real-time (with video). Gastric Cancer 2023 26 (2): 275-285.
(4) The authors should compare the proposed AI algorithm with other algorithms.
(5) The authors should analyze the experiment results in detail. In fact, it is difficult to understand
why the proposed method is a good one.
(6) English writing should be improved.
Review for 10.1186/s12876-024-03156-4 (2024)

Title: Reading of Small Bowel Capsule Endoscopy After Frame Reduction Using an Artificial
Intelligence Algorithm
Version: 2 Date: 24 Oct 2023
Reviewer's report:
I appreciated the contributions of the authors on “Reading of Small Bowel Capsule Endoscopy
After Frame Reduction Using an Artificial Intelligence Algorithm” and believe that it is
promising. At the same time, I identified some issues that require the authors' attention.
# The content of the manuscript should be described topically (section break).
# The description of the proposed method is more understandable if, it has a framework. Design
framework for the proposed method.
# How does the proposed AI algorithm work?
# The results were compared with the AI non-user group and the AI user group. It is more
reasonable if the proposed method is compared with related state-of-the-art methods.
# Would you check the performance proposed method on the publicly available benchmark
dataset (e.g Kvasir-Capsule, a video capsule endoscopy dataset)?
# Results visualization and description also need some standard tools.
Review for 10.1186/s12876-024-03156-4 (2024)

Title: Reading of Small Bowel Capsule Endoscopy After Frame Reduction Using an Artificial
Intelligence Algorithm
Version: 4 Date: 15 Dec 2023
Reviewer's report:
In the Discussion section, the authors said “software processing that can be performed
simultaneously with AI filtering during SBCE reading is required”. What does it mean?
Review for 10.1186/s12876-024-03156-4 (2024)

Title: Reading of Small Bowel Capsule Endoscopy After Frame Reduction Using an Artificial
Intelligence Algorithm
Version: 5 Date: 16 Jan 2024
Reviewer's report:
In the Discussion section, the authors said “In this study, 3 cases 3 cases had diagnostic
differences between the two examiners”. Duplicate words should be removed.
In the Discussion section, the authors said “However, in this study, the SBCE reading was
performed using the same software viewer, even after AI processing”. A period should be added
at the end of the sentence.
Review for 10.1186/s12876-024-03173-3 (2024)

Title:  Impact of insomnia upon inflammatory digestive diseases and biomarkers: a two-sample
mendelian randomization research on Europeans
Version: 1 Date: 25 Sep 2023
Reviewer's report:
The article has certain clinical meaning, and I hope to verify the results of the article again with
Meta-analysis.
Review for 10.1186/s12876-024-03173-3 (2024)

Title:  Impact of insomnia upon inflammatory digestive diseases and biomarkers: a two-sample
mendelian randomization research on Europeans
Version: 1 Date: 18 Oct 2023
Reviewer's report:
Nice study. It requires minor revision.
Delete one “and” from the title.
Remove the word “causal” from the entire manuscript, in the absence of prospective controlled
mechanistic exploration. Modify the conclusion accordingly.
Steps of data collection from the public domain need to be mentioned.
Necessary permission/waiver for analysing publicly available data from the institution of
authors, as applicable
Discussion length can be reduced.
There is some formatted text in Table 4 and in other places. Kindly share a clean manuscript.
Review for 10.1186/s12876-024-03170-6 (2024)

Title: A Comprehensive Study on Non-Cancer-Related Mortality Risk Factors in Elderly
Gastric Cancer Patients Post-Curative Surgery
Version: 2 Date: 13 Dec 2023
Reviewer:  Chikara Kunisaki
Reviewer's report:
Major comments
The topic of this study is interesting and important. However, there are some ambiguous and
insufficient data. Some data are also missing.
I wonder there were some studies dealing with same topic. What is new and different?
It is more useful to show clinically available suggestions based on the present study.
Minor comments
1. A total of 684 patients underwent curative resection. However, non-curative resection was
excluded from the study. Were patients without curative resection included in 684 patients?
In Results section, Of the 689 patients diagnosed with pStageI-III gastric cancer during the study
tenure, 603 underwent curative resection.
It is so confused. Please comprehensively describe this issue.
2. Please clearly and concisely describe the method of multivariate analysis.
3. Please clearly define the pneumonia and respiratory failure. What is the difference between
the two groups?
4. P9 L5, those who perished from other ailments.
Please concretely describe this. I wonder it is better to describe “non-cancer-related death” to
improv the readability.
5. What is the duration after surgery in alive patients without recurrence? It is necessary to
strictly define the follow-up time after surgery without recurrence. If the follow-up time is
longer, recurrence would be detected in a subset of population.
6. Authors used “overall complications” as a risk factor. I wonder many readers want to know
the correlation of > C-D II or III complications and non-cancer related death. Please re-analyze
this issue.
7. In general, it is important to avoid the repetition of the contents in the text, which is shown
in the tables. Authors frequently repeated the same contents in the text. Therefore, it is better to
summarize the important points in the text.
8. In Discussion section, authors mentioned about the superiority of minimally invasive surgery.
However, authors could not show the advantages of this approach in this study. It is necessary
to discuss the reason why there was no difference in this study.
9. P12, L2-4, In the context of our study, integrating CGA ------ directed interventions to alleviate
these risks.
We need more concrete suggestions. What can we clinically perform in daily practice according
to the results of this study?
10. Conclusion is not based on the outcomes of this study. This is like a textbook description. It
is necessary to conclude something new future perspectives based on the results of this study.
11. The information of adjuvant chemotherapy is important. Please show us this issue.
Review for 10.1186/s12876-024-03170-6 (2024)

Title: A Comprehensive Study on Non-Cancer-Related Mortality Risk Factors in Elderly
Gastric Cancer Patients Post-Curative Surgery
Version: 2 Date: 20 Dec 2023
Reviewer:  Manabu Ohashi
Reviewer's report:
Reviewer really appreciates having an opportunity to evaluate this manuscript titled A
Comprehensive Study on Other Disease Mortality Risk Factors in Elderly Gastric Cancer
Patients Post-Curative Surgery” written by Dr. Ushimaru et al. The manuscript is well written,
and the conclusions were properly derived from the results of this study. However, the study
has critical flaws, such as a single-institutional, retrospective study and small-sized study.
Furthermore, the study may have an essential problem. Reviewer would like to provide the
authors with some comments listed below.
1. First of all, the main results of this study: age (older age), BMI (malnutrition), and overall
complications were independent prognostic factors in elderly patients with curatively resected
gastric cancer, are quite natural. Reviewer believes that these factors may be prognostic factors
in elderly patients with another disease. Furthermore, these factors may be generally associated
with death of elderly people. Physicians are always concern that elderly patients, especially much
older, malnutritional patients or those with other comorbidities after gastrectomy get another
disease. Thus, reviewer is worried about whether the results of this study are new information
for potential readers. The authors should clearly describe in the introduction section what the
results have been reported regarding such an area so far, what information is insufficient and
what the authors will newly elucidate in this study. Moreover, in the discussion section, the
authors should also clearly describe how the information obtained from this study is different
from the past information, what may generate the differences between the results of present and
past studies and how the new information is useful in daily practice. If the authors can clearly
state such things, the study may be valuable even though it is a single-institutional, retrospective
and very-small-sized (only 33 patients were the final target) study.
2. In the multivariate analysis, the authors used the 4 variables. However, less than 10% of
the event number should be input to multivariate analysis generally. Otherwise, overfitting
phenomena will occur. In this study, the event (other-cause-death) number was 33. Thus, 3 or
less variables should be used in the multivariate analysis.
3. “Death within 5 years from non gastric cancer related death” is described at the bottom of
Figure 1. The word “death” is duplicated. A correction may be proper. The number of patients
at risk should be described in the Kaplan-Meyer’s curves.
Review for 10.1186/s12876-024-03162-6 (2024)

Title: Investigating the shared genetic architecture between multiple Primary sclerosing
cholangitis and inflammatory bowel diseases: A Mendelian randomization study
Version: 0 Date: 26 Dec 2023
Reviewer's report:
In this study, the authors investigated the causal associations of genetically predicted primary
sclerosing cholangitis (PSC)  with Inflammatory bowel disease (IBD).
Genetic variants associated with the genome-wide association study (GWAS) of PSC were used
as instrumental variables. The statistics for IBD, including ulcerative colitis (UC), and Crohn’s
disease (CD) were derived from GWAS.
Five methods were used to evaluate the effects of genetically predicted PSC on IBD, including
MR Egger, Weighted median (WM), Inverse variance weighted (IVW), Simple mode, and
Weighted mode. They found that genetically predicted PSC was significantly associated with
an increased risk of UC. However, none of the MR methods found significant causal evidence
of genetically predicted PSC in CD. They concluded that the study corroborated a causal
association between genetically predicted PSC and UC but did not between genetically predicted
PSC and CD.
The study is of interest, however, some issue should be addressed.
1) Methods: the authors reported that the summary statistics of PSC, UC, and CD was
derived from the IEU Open GWAS project. However, no clinical informations are provided.
In particular, both IBD and PSC, are frequently associated to other autoimmune diseases and
this might be significantly affected by a different genetic background. Therefore, since this my
introduce an unintetional selection bias, the comparison should consider homogeneous patient
groups.
2) Discussing the genetic factors associated with PSC, the authors inluded two references (ref 43:
J Immunol Res 2014, 2014:921285,  and 51: Clin Rev Allergy Immunol 2015, 48(2-3):316-321.)
that, however, refer to two studies of primary biliary cirrhosis patients (and not PSC patients).
3) discussing the impact of genetic factors in immune system, the authors should also
recall the role of genetic background in the serum antibody development. In this regard, the
authors should also discuss the likely role of genetic factors in the development of serum
antibodies found in diverse immune-mediated diseases. In particular, it is well known that
patients with UC develop serum Anti-Saccharomyces cerevisiae  antibodies (ASCA), which,
however, are also found in patients with celiac disease (Aliment Pharmacol Ther. 2005
Apr 1;21(7):881-7. doi: 10.1111/j.1365-2036.2005.02417.x.; Gut. 2005 Sep;54(9):1232-6. doi:
10.1136/gut.2004.060228.) and autoimmune liver diseases as previously demonstrated (Clin
Exp Immunol. 2003 Jun;132(3):473-6. doi: 10.1046/j.1365-2249.2003.02166.x.).
Review for 10.1186/s12876-023-03114-6 (2024)

Title: Effectiveness of a Thrombin-gelatin Flowable for treating severe liver bleeding: An
experimental study
Version: 2 Date: 27 Oct 2023
Reviewer's report:
The authors have conducted an experimental study on hemostasis in liver injury comparing
hepa=c packing as standard procedure versus Floseal applica=on as the hemosta=c method. A
swine model with 20 animals was used. Twelve animals were in the standard group and 8 in
the Floseal group.
The manuscript is easily understandable and the criteria of the trial are clearly described. The
contents and the goal of the study are important and the methods used and the results achieved
are worthwhile of being published.
Nevertheless, there are several points that need the aIen=on of the authors to improve the quality
of the manuscript.
- In the introduc=on sec=on of the paper the authors start with a descrip=on of the possible
difficul=es of hemostasis in elec=ve liver surgery and compare this to hemostasis in liver trauma.
Hemostasis in both elec=ve liver surgery and severe liver trauma are significantly different. In
severe liver trauma the pa=ents are cold, acido=c and have impaired coagula=on - they need
prompt aIen=on and effec=ve hemostasis that will be mostly established by adequate packing
within a damage control concept. This important factor is not the case in an elec=ve seQng. The
authors’ seQng in this trial is equivalent to elec=ve liver surgery. Although the lessons of this
trial can be perfectly adapted to the situa=on of severely injured pa=ents with ac=vely bleeding
liver lacera=on, the trial itself is a unique mixture of an elec=ve surgical seQng and a therapeu=c
approach to “packing” that will predominantly be used in trauma. In the introduc=on of the
manuscript, these circumstances should be clearly outlined.
- The only exclusion criteria: “Animals in which one of the suprahepatic veins had not been
selectively injured were excluded from the study” is not clearly understandable. The authors
should re-write this sentence and clarify the probable reasons why an animal did not qualify.
How many animals were used to perform the trial in 20 animals? Were there some that
unexpectedly died before, during or after intubation or during the surgery?
- The randomiza=on process is not clearly described. The authors do not state at which =mepoint
the randomiza=on was made - before or during surgery- and if during the surgery, at which stage?
- The descrip=on of the experimental model should also include the age, weight and gender of
the animals.
- During the follow-up at 12, 60 and 120 minutes were only one or two packs removed from
over the injuries or all 10 pads? The authors should clarify if there were differences at different
=mepoints, which pads were removed first and why, if all pads were removed at each =mepoint.
Review for 10.1186/s12876-023-03114-6 (2024)

Title: Effectiveness of a Thrombin-gelatin Flowable for treating severe liver bleeding: An
experimental study
Version: 2 Date: 07 Nov 2023
Reviewer's report:
In this submission Dr. Sanchez del Valle and co-authors present data comparing the effectiveness
of a flowable hemostat with that of standard wound packing in a novel hepatic vein injury model.
The submission could be improved by the following:
1. The method of randomization for the treatment methods should be described in more detail
with respect to if it was after the wounds were created as well as the days on which the animals
underwent the procedure and the specific surgeons doing each animal.
2. Clarify why was 12 minutes of pressure applied to the wounds in the flowable group and not
in the packing group. Does the instructions for use of the flowable recommend 12 minutes of
pressure application?
3. Should the pressure time be added to the application time for the flowable?
4. Explain how was blood collected for measurement of weight of blood lost.
5. Use of capitals in titles and body of paper could be standardized.
6. The primary endpoint results of the study could be presented in tabular form.
7. The assignment of Level of Evidence I could be explained as this level is often reserved only
for randomized controlled studies.
8. Why were the methods of determining blood loss in the first 12 minutes in the two groups
different?
Review for 10.1186/s12876-023-03114-6 (2024)

Title: Effectiveness of a Thrombin-gelatin Flowable for treating severe liver bleeding: An
experimental study
Version: 3 Date: 29 Nov 2023
Reviewer's report:
Dr. Sanchez del Valle and co-authors present have submitted a revised manuscript based on the
comments of the three reviewers. The submission could be improved by:
1. Clarifying if the surgeons were blinded to the treatment group until after the liver injury was
created. If the surgeons were not blinded through the performance of the injury to the liver, how
was bias in performance of the injury avoided?
2. Further clarification of the time of pressure application would be helpful. The authors state that
the manufacturer’s instructions were followed. This does not seem accurate as the manufacturers
recommend two minutes of pressure application after product application and that reapplication
of product can be repeated followed by pressure as necessary if hemostasis is not achieved after
the initial two minutes of pressure. Did the authors check at two minutes to see if hemostasis was
achieved? How was the 12 minute time for pressure chosen? Please clarify why the extended
pressure application time not suggested by the manufacturer was not added to the application
time for both the flowable and the control agent.
Review for 10.1186/s12876-023-03114-6 (2024)

Title: Effectiveness of a Thrombin-gelatin Flowable for treating severe liver bleeding: An
experimental study
Version: 5 Date: 27 Dec 2023
Reviewer's report:
Dr. Sanchez del Valle and co-authors present have submitted a revised manuscript based on the
previous comments of the reviewers.
The authors have completed substantial additions and corrections. In this form the manuscript
can be accepted for publication.
Review for 10.1186/s12876-024-03151-9 (2024)

Title: The pertinence of gastric cancer and interleukin 10-819 single nucleotide polymorphisms:
a meta-analysis and systematic review
Version: 1 Date: 16 Nov 2023
Reviewer:  Reza Alizadeh-Navaei
Reviewer's report:
This study investigates the association between gastric cancer and a single nucleotide
polymorphism (SNP) of interleukin-10 (IL-10) promoter -819 (rs1800871) through a meta-
analysis. The authors retrieved relevant articles from various databases up to March 2022 and
analyzed data from 15 articles, including a total of 7779 patients. The study found no correlation
between gastric cancer and IL-10 -819 in the recessive, co-dominant, or dominant models, but,
in the allelic model, there was a significant correlation between gastric cancer and IL-10 -819.
The authors emphasize the need for more large cohort studies to confirm these results. However
there were some minor comments for this manuscript:
1- Field of search strategy was not mentioned.
2- In statistical section, Authors mentioned, "Mean difference (MD) was generated as effect-
size for continuous variants" this despite the fact that, there was not any related finding in result
section. Additionaly, authors in result say that " Publication bias is qualitatively tested by funnel
chart, and quantitatively estimated by Begg and Egger's tests. No significant asymmetry was
observed in the funnel chart, which indicated that our findings were not affected by publication
bias" but in statistical section they say that " Publication bias was assessed by Egger’s test". This
inconsistency needs edition.
3- Number of document from each database should be added in Prisma flowchart.
4- NOS score of each individual study should be added in table 1.
5- It seems that authors extract crude rate, additionally, they must be extract and analysis the
adjusted OR for related variables.
Review for 10.1186/s12876-024-03151-9 (2024)

Title: The pertinence of gastric cancer and interleukin 10-819 single nucleotide polymorphisms:
a meta-analysis and systematic review
Version: 1 Date: 02 Dec 2023
Reviewer's report:
A lot of meta-analysis has been published previously about the association of  IL-10
polymorphisms with GC risk, which make it unnecessary for the analysis, especially in post-
GWAS era.
Review for 10.1186/s12876-024-03151-9 (2024)

Title: The pertinence of gastric cancer and interleukin 10-819 single nucleotide polymorphisms:
a meta-analysis and systematic review
Version: 3 Date: 09 Jan 2024
Reviewer:  Reza Alizadeh-Navaei
Reviewer's report:
Thanks for revised manuscript
Review for 10.1186/s12876-024-03147-5 (2024)

Title: Comparative efficacy and safety of Sofosbuvir/Velpatasvir and Danoprevir for the
treatment of chronic hepatitis C: the real-world data in China
Version: 0 Date: 03 Jun 2023
Reviewer:  Markus Reiser
Reviewer's report:
This manuscripts describes a retrospective analysis of the efficacy of velpatasvir/sofosbuvir
and danoprevir based treatments for chronic hepatitis C virus infections.  I have the following
comments:
1. The patient cohorts are quite heterogenous including  different HCV genotypes, fibrosis stages
and even HIV coinfections. Moreover, the treatment regimens seem to be manifold including
ribavirin, ritonavir and Peg-interferon. The patient characteristics and  applied treatment
regimens should be described in more detail.
2. The higher rate cirrhosis in the Vel/Sof group ist likely due to the lack of approval of
danoprevir for patients with cirrhosis. Nevertheless, some patients with cirrhosis and non-GT1-
infections were treated off-label with danoprevir based regimens. SVR and safety data in these
subgroups should be presented in more detail.
3. Table 2 contains superfluous routine laboratory data and should be shortened. Reference
ranges should be included.
4. The values presented in table 3 are not clear to me: Why does 64 of 82 or 31 of 66 patients
add up to a 100% SVR?
5. The discussion should be focused on the efficacy data and safety of the regimes. More
information regarding efficacy and safety in the off-label treated patients should be presented.
The discussed AFP and cirrhosis aspects are of limited value since these differences are likely
due to the approved indications.
6. Figure 1 can be ommitted.
7. Minor comment: I recommend against using brand names, therefore, Vel/Sof should be used
instead of epclusa.
Review for 10.1186/s12876-024-03147-5 (2024)

Title: Comparative efficacy and safety of Sofosbuvir/Velpatasvir and Danoprevir for the
treatment of chronic hepatitis C: the real-world data in China
Version: 0 Date: 03 Jul 2023
Reviewer's report:
This study investigated head-to-head comparison between a well-established DAA HCV
treatment represented by Epclusa vs a newly approved Chinese DAA called Danoprevir. The
authors compared two groups of patients treated with both treatment regimens. There are couple
of issues needs to be addressed:
1- The mode of action of Danoprevir needs to be added in the introduction.
2- The SVR rate in Danoprevir's group needs to  breakdown based on the genotype.
3- Table 3 is not clear, the numbers of patients with negative RNA at 4W and EOT and SVR12
do not add up to the total number for each group.
Review for 10.1186/s12876-024-03147-5 (2024)

Title: Comparative efficacy and safety of Sofosbuvir/Velpatasvir and Danoprevir for the
treatment of chronic hepatitis C: the real-world data in China
Version: 0 Date: 10 Jul 2023
Reviewer:  Chun-Ming Hong
Reviewer's report:
Nice work, congratulations!
I have some comments and questions:
Comments:
1. In Line 37 of Abstract, “real word study” should be “real world study”.
2. What are the percentages of HBV co-infection in ECS and DNV groups?
3. What are the percentages of HIV co-infection in ECS and DNV groups?
Review for 10.1186/s12876-024-03147-5 (2024)

Title: Comparative efficacy and safety of Sofosbuvir/Velpatasvir and Danoprevir for the
treatment of chronic hepatitis C: the real-world data in China
Version: 2 Date: 01 Nov 2023
Reviewer:  Chun-Ming Hong
Reviewer's report:
The revised manuscript improved much.
I have two suggestions: firstly, the format in Discussion should be uniformed. Secondly, in Line
251, "Bedsides" should be  "Besides".
Review for 10.1186/s12876-024-03147-5 (2024)

Title: Comparative efficacy and safety of Sofosbuvir/Velpatasvir and Danoprevir for the
treatment of chronic hepatitis C: the real-world data in China
Version: 3 Date: 19 Jan 2024
Reviewer:  Chun-Ming Hong
Reviewer's report:
This study provides real-world comparisons between a new drug and an established DAA.
However, the questions that I raised (the percentages of HBV and HIV co-infection) were not
elucidated.
Review for 10.1186/s12876-024-03121-1 (2024)

Title: Development of A Prediction Model for Predicting the Prevalance of Nonalcoholic Fatty
Liver Disease in Chinese Nurses: The First-Year Follow Data of a Web-Based Ambispective
Cohort Study
Version: 2 Date: 16 Nov 2023
Reviewer's report:
The aim of this study was to develop and validate a prediction model to predict the incidence of
NAFLD in female nurses. The strength of this study was to collect various information including
demographic characteristics, work situation, and daily lifestyle. However, there are still several
shortcomings.
1. In line 106, the main outcome is the incidence of NAFLD. However, the flow chart did
not show that the prevalent NAFLD were excluded initially. In addition, the author should
mention why the cohort was classified into two sets. If the prediction model was made from
the development set, the author should explain why the prediction was not made from the total
participants.
2. I think Table S1 is important and should be included in the manuscript after reorganized.
3. In line 154, the author mentioned that 27 indicators were recognized as risk factors for NAFLD
indicators, and the detailed parameters of the characteristics in univariate analysis are presented
in Table 3. However, Table 3 only included 21 factors.
4. In line 160, the author mentioned that 11 indicators were recognized as risk factors for NAFLD
development in Table S1. However, only 8 indicators were reported in line 162. Then, the
NAFLD risk nomogram was built based on the 7 independent predictors. The real number of
indicators should be clarified.
5. The strength of this study was the factors related to work situation and lifestyle. However, the
author discussed many laboratory tests and the important non-laboratory factor of the shift work
were only mentioned in line 236-238. The shift work is most important finding in this study,
which may be neglected by other researches.
6. The author reported that AST and Tbil were protective indicators of NAFLD incidence, which
is controversial. The author should provide more explanation or evidence to support.
7. There are minor suggestions. First, the content of Table 1 can be integrated into the methods
and Table 1 may be reserved in the supplement. Second, in Table 2, the data of ALT should
be revised.
Review for 10.1186/s12876-024-03121-1 (2024)

Title: Development of A Prediction Model for Predicting the Prevalance of Nonalcoholic Fatty
Liver Disease in Chinese Nurses: The First-Year Follow Data of a Web-Based Ambispective
Cohort Study
Version: 2 Date: 27 Nov 2023
Reviewer's report:
This is cohort study aimed to develop and validate a prediction model to predict the incidence
of NAFLD based on demographic characteristics, work situation, daily lifestyle and laboratory
tests in female nurses in the population China. I think the topic is interesting and contributive
to the epidemiology under an empirical approach quite valuable for clinical internal medicine
professionals.
Major concerns:
1. Statistical methods were described very well. Why the authors did not use stepwise logistic
regression in this study? The authors should clarify this concern.
2. Use of logistic regression regression is appropriate when using data with a common outcome.
Did the authors check with relative risk for this analysis? Please compare results of relative risk
and odds ratio.
3. In Supplementary Table, there existed inflation in odds ratio (Ca). The authors should clarify
this concern. PMCID: PMC8274998. I mean add a limitation in this study.
4. The authors should add some mechanism between risk factor and outcome in discussion
section.
5. Some references required updated.
Review for 10.1186/s12876-024-03121-1 (2024)

Title: Development of A Prediction Model for Predicting the Prevalance of Nonalcoholic Fatty
Liver Disease in Chinese Nurses: The First-Year Follow Data of a Web-Based Ambispective
Cohort Study
Version: 4 Date: 14 Dec 2023
Reviewer's report:
Thank authors for responding the previous suggestions and revising the manuscript accordingly.
There are still minor suggestions.
1. In line 250, the author mentioned that living with spouse and parents were associated with
higher risk of NAFLD. However, in table 2, living with spouse and parents were not significantly
related to NAFLD. Maybe it meant that living with solitary was associated with non-NAFLD.
The author should clarify the dispute.
2. In addition, in table 2, the classification of BMI was non-meaningful because it only meant that
BMI <18.5 was not related to NAFLD. The underweight people were essentially less likely to
have NAFLD. I suggested that the continuous variable of BMI replaced the categorical variable
in the logistic regression even though it could be not significant in the model.
3. The daily sleep time has caught my attention because the daily sleep time 7-8h was significant.
The author can reclassify this variable and the daily sleep time may be significant in the mode.
4. In line 232, the author mentioned that bilirubin was a protective factor against the occurance of
NAFLD. Could it be the reason that some participants with NAFLD have received treatments?
Review for 10.1186/s12876-024-03155-5 (2024)

Title: Safety and feasibility of minimally invasive gastrectomy following preoperative
chemotherapy for highly advanced gastric cancer
Version: 2 Date: 08 Nov 2023
Reviewer:  Chikara Kunisaki
Reviewer's report:
Major comments
This topic is important. However, there are some points to be addressed more clearly and to
be corrected.
Previously some studies reported similar outcomes. What are the most noteworthy points in this
study as compared to the previous studies?
Minor comments
1. Please clarify the definition of highly advanced gastric cancer. What is the difference between
highly advanced gastric cancer and advanced gastric cancer?
2. Please discuss the rationale to analyze the outcome in patients with cStage III and cStage IV
together.
3. In this study, an advanced large tumor is defined as one >cT3 and >5 cm. Usually, a large
tumor is defined as one >8 cm. Please discuss the rationale of the definition in this study.
4. This is a retrospective study. How did authors obtain the IC for this study? Opt-out?
Please clarify this issue.
5. Multivariate analysis was performed using variables with a P-value <0.10 in the univariate
analysis.
Is this method statistically correct? Please consult the statistician.
6. Table 1, 2, and 5, we need more sophisticated tables.
7. Please show the precise information of adjuvant chemotherapy.
8. In Table 3. Please add the unit to BMI.
9. In this study, authors argued the superiority of RG for splenectomy. It may be true as the multi-
articulated joint angle of RG is a great surgical advantage. However, RG was introduced after the
sufficient experience of LG. therefore, the surgical learning curve must affect the outcomes. It is
necessary to discuss this important issue. Moreover, the experience of the surgeons participated
in this study is also important. Although authors argued the surgeon’s qualification, it is better
to offer the information of the experiences of the surgeons in each group.
10. Authors raised four findings. Of these, authors pointed out the safety and feasibility of
minimally invasive surgery as first point, and also pointed out those regardless of the surgical
method as third point. These can be integrated into one. Please reconsider this issue.
11. In combination with more effective regimens of preoperative chemotherapy, minimally
invasive surgery may play an important role in multidisciplinary treatment in the future.
Minimally invasive surgery can be changed to RG? Please reconsider this issue.
12. Ethics approval and informed consent to participate
---- and written informed consent was obtained from all individual participants included in this
study.
Is it true? I wonder some participants died of gastric cancer or other diseases. Is it possible to
obtain the written informed consent from all patients? Please clarify this issue.
Review for 10.1186/s12876-024-03155-5 (2024)

Title: Safety and feasibility of minimally invasive gastrectomy following preoperative
chemotherapy for highly advanced gastric cancer
Version: 2 Date: 14 Nov 2023
Reviewer's report:
This single institutional retrospective study sough to evaluate safety and feasibility of minimally
invasive gastrectomy after preoperative chemotherapy for gastric cancer. The authors performed
logistic regression analysis for risk factors of postoperative complication and concluded robotic
surgery may be better than laparoscopic surgery specifically in the case of total/proximal
gastrectomy. The analyses seem performed properly and the manuscript is well written.
I have few minor comments as mentioned bellow.
Abstract, Results and page 10, line 20-23
The authors showed only P values for the logistic regression analysis, but it doesn’t help readers
understand how big the correlation was. Odds ratios and confidence intervals are more important.
Page 6, line 9-10
“S-1 plus cisplatin” seems duplicated.
Page 8, line 5
“Sight” should be “slight”.
Page 9, line 6-7
The authors should indicate the number of patients in whom conversion surgery were attempted
and the number of patients in whom R0 resection was capable among them.
Page 12, line 16
“DVSS” should be spelled out.
Page 13, line 3
“JCOG1001” should be “JCOG0110”.
Page 13, line 3
The reference number [38] should be [39].