JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-01833-2 (2021)

Title: Natural killer cell activity is a risk factor for the recurrence risk after curative treatment
of hepatocellular carcinoma
Version: 1 Date: 13 Apr 2021
Reviewer's report:
This study aimed to investigate the role of natural killer (NK) cell activity in determining
the outcomes of patients with HCC. The authors demonstrated that the IFN-# producing NK
cell proportion seemed to be lower in patients with advanced stage HCC when compared to
those with early stage HCC. Moreover, for patients who underwent curative therapy, the IFN-#
producing NK cell proportion < 45% at 1 month after treatment was associated with an increased
risk of recurrence after therapy.
Immunopathogenesis of HCC has not been clearly elucidated, and this article is very timely in
that it explains, at least partly, the important role of NK cells (the most important innate immune
cells for the cancer control) in HCC control.
1. The authors seem to have used pan-T/NK cell stimulants for the NK cell stimulation and ICCS
for IFN-gamma, because the authors divided the population into patients with IFN-g+NK >45%
or <45%.  Representative FACS dotplots for IFN-gamma staining (with appropriate gating) of
NK cells with isotype control should be presented as a main figure.
2. In chronic HBV infection, NK cells have reported to show cytotoxicity against HBV-
specific CD8 T cells to weaken adaptive immune responses. Moreover, it was also reported
that peripheral NK-cell activity (cytokine secretion and cytotoxicity) in immune active HBV
infection has a negative correlation with  (Li et al. PLoS One. 2014;9:e86927). As a majority
of included patients had chronic hepatitis B as an underlying liver disease in this study, patients
should be stratified according to the serum HBV DNA levels.
3. It would be better to define primary outcome more precisely: Was it a recurrence-free survival
or time-to-progression? It might be an important issue since patients with advanced or end-stage
HCC were also included.
4.  In this study, there were no significant changes in IFN-# producing NK cell proportion from
baseline to 1 month after curative treatment. However, only the post-treatment, but not baseline
IFN-# producing NK cell proportion < 45% was associated with tumor recurrence. It is suggested
to provide the Figures to depict the correlation between baseline and post-treatment NK cell
activity.
5. Minor spelling and spacing errors are noted throughout the manuscript. Moreover, awkward
expression are noted. One more round of English editing should be performed.
Review for 10.1186/s12876-021-01833-2 (2021)

Title: Natural killer cell activity is a risk factor for the recurrence risk after curative treatment
of hepatocellular carcinoma
Version: 1 Date: 17 Apr 2021
Reviewer's report:
In this study, Lee et al. investigated the association between NK cell activity and the recurrence
risk of HCC. They examined IFN-g production from peripheral blood NK cells at the time of
diagnosis and 1 month after treatment. Importantly, they found that patients with low NK cell
activity (<45% IFN-g producing NK cells) at 1 month after treatment showed a significantly
higher HCC recurrence rate than patients with high NK cell activity. They concluded that
decreased NK cell activity is associated with the increased recurrence risk of HCC after
treatment. I have several technical comments.
1. The authors need to present representative FACS plots for IFN-g production from NK cells.
It will be better to show examples of high and low NK cell activities, respectively.
2. In this study, PBMCs were stimulated with Leukocyte Activation Cocktail (BD Biosciences)
to induce IFN-g production from NK cells. Leukocyte Activation Cocktail (BD Biosciences)
includes PMA and ionomycin and can stimulate not only NK cells but also T cells. It means that
the authors can analyze IFN-g production from T cells without further experiments. They can
re-analyze their FACS data files by gating CD3+ T cells. Please analyze a possible association
of T cell activity with stage and recurrence risk of HCC. This analysis will validate whether the
conclusion of this study is NK cell-specific or not.
3. In supplementary Figure 2, representative FACS plots for cases with preserved (A) or
decreased (B) NK cell proportion are presented. However, it seems that there is no difference in
NK cell proportion between the two cases. It seems that cell viability is poor in the second case
(B). What was cell viability of PBMC in general? Regarding cell viability, my above comment
(#2) is important because poor cell viability results in poor IFN-g production not only from NK
cells but also from T cells.
Review for 10.1186/s12876-021-01837-y (2021)

Title: Sofosbuvir/velpatasvir is an effective treatment for patients with hepatitis C and advanced
fibrosis or cirrhosis in a real-world setting in Taiwan
Version: 2 Date: 02 May 2021
Reviewer's report:
This study focuses on a real life treatment experience with SOF/VEL in chronic hepatitis C
infection. The peculiarity of this work is that it is based on a study completely conducted in
Asia. The results are in keeping with others published in Europe or derived from global real
life experiences. However, there are some aspects that need to be presented and discussed in
more detail.
The Authors say that only few patients were treated with the combination of SOF/VEL
plus  ribavirin. In order to contribute to the debate on the addition of ribavirin to SOF/VEL
combination in patients with cirrhosis, recommended by international guidelines in Europe, it
would be important to specify how many patients with Child Pugh-Turcotte classes (CTP) A or
B were included in this study.  Please, include this information in both text and Tables. Were
only CTP B treated with the addition of ribavirin, or not?
Were among patients who prematurely discontinued treatment or did not complete the post
treatment follow up, subjects receiving ribavirin? Was any dose adjustment of ribavirin
required? Are data on adherence available?
Review for 10.1186/s12876-021-01837-y (2021)

Title: Sofosbuvir/velpatasvir is an effective treatment for patients with hepatitis C and advanced
fibrosis or cirrhosis in a real-world setting in Taiwan
Version: 5 Date: 12 May 2021
Reviewer's report:
Would you please report in a separate table number and treatment of  cirrhotic patients in CTP
B and cirrhotic patients on CTP C classes?
Review for 10.1186/s12876-021-01794-6 (2021)

Title: Serum pepsinogen levels in different regions of China and its influencing factors-a
multicenter cross-sectional study
Version: 1 Date: 27 Feb 2021
Reviewer's report:
TITLE
Serum pepsinogen levels in different regions of China and its influencing factors-a multicenter
cross-sectional study
Authors
Yuling Tong; Hongguang Wang; Yi Zhao; Xueqiang He; Hongwei Xu; Hong Li; Ping Shuai;
Lirong Gong; Hongbo Wu; Hongzhi Xu; Yinhu Luo; Dong Wang1; Shizhu Liu2; Zhenya Song
In their scientific manuscript, the Author further test the predictive value of gastric serology
(Pepsinogen-I-II, and Pepsinogens ratio) in predicting the gastric atrophy-associated cancer risk
The major interest of the achieved results is in the variability of the predicting value of serology
according to the risk factors as registered in different Chinese regions/populations.
This feature (not completely new) is fully supported by the results obtained in the different
populations, as recruited from different Chinese regions (overall study population: 1590
[including 254 individuals from South China, 574 from East China, 210 from Southwest China,
332 from Northeast China, and 220 from Central/Northern China]).
The authors conclude that the cut-off value for PgI/PgII ratio should be adjusted according to the
regional prevalence of H. pylori infection, the socioeconomic, dietary habits, and ethnic profile
of the addressed populations.
When this variability is taken into account, serology may be usefully applied as a subsidiary
method in the initial approach to gastric cancer secondary prevention ultimately increasing the
appropriateness of the endoscopy histology procedures.
The manuscript includes interesting data.
References are basically adequate
Some problems in English editing should be addressed.
While the correlation between histology (OLGA Staging)  and PgI/PgII ratio is expected not
highly informative (due to the “limited” protocol of biopsy sampling), it would have been
interesting to explore the correlation between PgI/PgII ratio and OLGA stages (Low-risk OLGA
0-I-II stages versus High-risk  OLGA III-IV stages; see potential references PMID: 30333540,
PMID: 29306868)
Review for 10.1186/s12876-021-01794-6 (2021)

Title: Serum pepsinogen levels in different regions of China and its influencing factors-a
multicenter cross-sectional study
Version: 1 Date: 17 Mar 2021
Reviewer's report:
The paper appears interesting making differences between regions of China as regards
pepsinogens levels and PGI/PGII ratio and for point out the rate of atrophic gastritis and more
severe OLGA staging has screening test in healthy population.
Nevertheless, I’m quite confuse about some points, in particular the relationship between
pepsinogens differences in various areas and possible involved factors. For instance, Pepsinogen
II is claimed worldwide as marker of inflammation of gastric mucosa, been related with H.p.
infection, but in the study the more elevated values of PGII are find in northeast and central north,
while the higher rate of H.p. infection where in southern and eastern. As regards the supposed
relationship between increase in PGI levels and presence of minority ethnic groups, the authors
mean genetics or environmental factors, like dietary, smoking habit, etc…
Some questions:
1 What about levels of PGI and ratio in subjects affected by atrophic gastritis (17.3%)?
2 What about the PGI values in patients with pictures of OLGA III/IV (2.5%)?
Review for 10.1186/s12876-021-01794-6 (2021)

Title: Serum pepsinogen levels in different regions of China and its influencing factors-a
multicenter cross-sectional study
Version: 2 Date: 08 Apr 2021
Reviewer's report:
The authors answer satisfactorily to all questions point by point. The results are interesting and
important to point out the usefulness of different cut-off in serum parameters, according to with
regional specificity.
Review for 10.1186/s12876-021-01794-6 (2021)

Title: Serum pepsinogen levels in different regions of China and its influencing factors-a
multicenter cross-sectional study
Version: 2 Date: 25 Apr 2021
Reviewer's report:
Manuscript title:
Serum pepsinogen levels in different regions of China and its influencing factors-a multicenter
cross-sectional study
Authors: Yuling Tong, et al .
_____________
Comments:
The present R1-version of the above-mentioned manuscript has been sensibly improved and all
the major criticisms, as previously provided, have been consistently addressed.
Review for 10.1186/s12876-021-01839-w (2021)

Title: Efficacy and safety analysis of dexamethasone-lipiodol emulsion in prevention of post-
embolization syndrome after TACE: a retrospective analysis
Version: 2 Date: 07 May 2021
Reviewer:  Élia Coimbra
Reviewer's report:
For conventional TACE, using dexamethasone to reduce the pos-embolization syndrome  makes
a lot of sense, and this work proved that it is done effectively and without complications. I hope
that other centers can also prove this.
Review for 10.1186/s12876-021-01839-w (2021)

Title: Efficacy and safety analysis of dexamethasone-lipiodol emulsion in prevention of post-
embolization syndrome after TACE: a retrospective analysis
Version: 2 Date: 29 May 2021
Reviewer's report:
English language should be double checked by a native speaker.
I have concerns about the selection of patients and methodology.
Some parts like the results section are incomprehensible in the current style.
Abstract
The results section should be rewritten and rephrased. Please put exact p values. Replace VS
with vs.
Materials and Methods
« 300–500 um gelatin sponge particles » : how is it possible to have this exact size of sponge
particles ?
“Chemotherapeutic drugs used during surgery are divided into two types: (1) lobaplatin 50 mg;
(2) epirubicin 30 mg”: what was the proportion of patients with each of them ?
The technique of TACE (selective, lobar) should described more in detail. It can seriously impact
the incidence of PES.
Results
Should be completely rephrased.
Why does basic information section appear here ?
Discussion
Too long.
Tables
What is the sense of having 2 statistical tests in tables ?
Review for 10.1186/s12876-021-01773-x (2021)

Title: Is insulin the preferred treatment in persons with type 2 diabetes and liver cirrhosis?
Version: 1 Date: 18 Jan 2021
Reviewer's report:
The analysis of the glycemic control/ diabetes status is a major limitation.
This could be a significant confounding factor.
Requiring insulin treatment could have been a bias pointing towards a worse outcome
Hence the conclusion that the insulin users had a worse outcome itself may be biased.
Review for 10.1186/s12876-021-01773-x (2021)

Title: Is insulin the preferred treatment in persons with type 2 diabetes and liver cirrhosis?
Version: 1 Date: 25 Jan 2021
Reviewer:  Mananjala Senanayake
Reviewer's report:
I felt it was a well written article which was suitably addressing the relevant clinical question
of the use insulin in compensated liver cirrhosis
May I suggest the following minor revisions to improve its suitability
1. Include that it is a retrospective cohort study
2. Includes that the definition of death includes patient no longer having coverage as a limitation
Very best wishes
Review for 10.1186/s12876-021-01773-x (2021)

Title: Is insulin the preferred treatment in persons with type 2 diabetes and liver cirrhosis?
Version: 1 Date: 08 Feb 2021
Reviewer's report:
This is a study involving a very large population addressing a relevant and interesting question.
The accuracy of data depends very much on accurate collection, since the study is based on
a database, albeit a national one. For example, the definition of 'death' is questionable. Also,
defining 'insulin user' with a minimum period of use of only 28 days is inadequate. There are also
a few typographical errors in the manuscript (lines 45 and 75). Although a prospective cohort
study can better address this research question this large retrospective analysis is a good attempt
to find answers to a problematic clinical question.
Review for 10.1186/s12876-021-01773-x (2021)

Title: Is insulin the preferred treatment in persons with type 2 diabetes and liver cirrhosis?
Version: 1 Date: 08 Feb 2021
Reviewer's report:
Please explain the Charlson comorbidity index (CCI) [15] and Diabetes Complication Severity
Index (DCSI) scores and whether the data required is present in your database
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 1 Date: 07 Mar 2021
Reviewer's report:
REVIEW
This is a well written paper regarding  the association of thromboelastography profile with the
severity of liver cirrhosis and portal venous system thrombosis(PVST).The authors evaluated
two cohorts with overall 166 cirrhotic patients.They compared thromboelastography(TEG)
parameters between cirrhotic patients with Child-Pugh class A and B/C, those with and without
decompensation, and those with and without PVST. They concluded that hypercoagulability
might not be related to more advanced stages of liver cirrhosis or presence of PVST  using a novel
definition of hypercoaguability and that there is a high rate of discordance between  reactive
time  and other thromboelastography parameters.
However ,there are some issues which should be addressed by the authors
1) Using different TEG facilities and reference ranges despite applying the same reagents makes
the evaluation of results between the two cohorts  precarious
2) It would be interesting to separately analyze the data for Child Pugh B and Child Pugh C
patients.Is there any particular reason for merging these two groups?
3) The study excludes cirrhotics with common complications of the disease that are more likely
to have a more severe disease
4) The exlusion criteria  preclude the most common risk factors for PSVT in cirrhotic patients
so the study population may not be  representative
5)  Also,what was the time limit for an abdominal surgery that made someone ineligible for
the study?
6) Authors should provide more information about the definition of hypercoagulability
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 1 Date: 21 Mar 2021
Reviewer:  Iliana Mani
Reviewer's report:
Dear Authors,
Cirrhosis has long been considered an acquired hemorrhagic disorder. However, in recent
years became clear that hemostasis in cirrhosis is rather “rebalanced”, as decreases in
procoagulant factors are accompanied by reduced levels of natural anticoagulants. Viscoelastic
tests significantly contributed to the better understanding of this complicated relationship,
providing information about the “in vivo” hemostatic procedure.
Thrombosis of the portal venous system occurs in a significant proportion of cirrhotic patients,
been more frequent in the advanced stages of liver disease. Although it is a well-known
complication, issues in regard to prognostic factors for its development, appropriate treatment
and duration of treatment are still under debate.
The current study is of great interest as it could improve our understanding about the
characteristics of hemostasis of patients presenting with portal venous system thrombosis and
subsequently to contribute to the better treatment or even prophylaxis of the vulnerable patients.
Major comments:
1) Authors should explain briefly the phases of hemostasis expressed by the variables of TEG
under study as well as the conventional coagulation factor(s) that are involved in each phase.
2) Fibrinogen is a key element for hemostasis. In TEG, its impairment leads to alternations both
of K and a-angle. Authors should mention levels of fibrinogen and study its correlation with
TEG parameters.
3) Authors should provide more information about the selection of criteria used to characterize
hypercoagulability as there is great discrepancy among the different studies and I did not find
a universal definition in regard to TEG.
4) A comparison between proportion of patients with values under or above the reference limit
would be significantly more informative than the comparison of median values between the
subgroups of interest.
5) Page 11, lines 221-223. R variable reflects the initiation of clot formation and is highly
dependent on coagulation factors. Both qualitative and quantitative platelets’ abnormalities are
accompanied by normal or near normal R. On the contrary, K and a angle are dependent mainly
on fibrinogen and MA on platelets. In my opinion, presence of shortened R should be highlighted
even if the retrospective design of the study does not allow comprehensive interpretation of
this result. Measurement of coagulation factors may reveal an explanation with implication in
clinical practice.
6) The manuscript needs extensive editing for grammar and syntax errors.
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 2 Date: 17 Apr 2021
Reviewer's report:
The manuscript has been properly revised and appropriate changes have been made by the
authors who also gave satisfactory answers to the reviewers' comments.
In my opinion the manuscript could be accepted for publication.
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 3 Date: 08 May 2021
Reviewer:  Iliana Mani
Reviewer's report:
Dear Editor,
I have only some minor comments to make.
Page 5, line 94.
Instead of “patients who received the drugs...” authors could write “patients who received
drugs...”
Page 5, line 89
Instead of “TEG parameters were shown” authors should write are shown
Page 8, line 170
Instead of “Compared those without” authors should write “compared to those without”
Page 12, line 262
Instead of “…only included the patients with the presence of gastroesophageal varices alone….”
Authors could write “…included only patients with gastroesophageal varices ….”
Page 12, line 243, 247, 249 and Page 13, line 266
I think that using “ may or might” is more appropriate than “should”
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 3 Date: 13 May 2021
Reviewer's report:
Although almost ready for publication this manuscript needs further proofreading.My comments
are as follows:
Page 4, Line 72. Instead of “patients who received the drugs with documented impact on
coagulation status” authors should write “patients who received drugs with documented impact
on coagulation status” (without the word  ‘’the ‘’ before the word ‘’ drugs’’)
Page 10, Lines 211-213. The statement “TEG can provide comprehensive information about
function and amounts of pro-coagulants, anti-coagulants, PLT, and cells and their interactions” is
not clear and could be replaced by the statement ‘’ TEG can provide comprehensive information
about function and amounts of pro-coagulants, anti-coagulants and PLTs as well as their
interactions’’
Page 11, Lines 239-240. Please rephrase the statement  “Notably, Huang et al. only included
the patients with the presence of gastroesophageal varices alone, but we did not limit the
complications or severity of liver cirrhosis” .It could be replaced by  the statement “Notably,
Huang et al.  included only patients with gastroesophageal varices  but we also included patients
with other complications of  liver cirrhosis ”
Review for 10.1186/s12876-021-01832-3 (2021)

Title: Association of Thromboelastography Profile with Severity of Liver Cirrhosis and Portal
Venous System Thrombosis
Version: 4 Date: 23 May 2021
Reviewer:  Iliana Mani
Reviewer's report:
Dear Editor,
I think that the manuscript, at its current form, is suitable for publication.
Review for 10.1186/s12876-021-01834-1 (2021)

Title: Comparison of the operative outcomes and learning curves between laparoscopic and
“Micro Hand S” robot-assisted total mesorectal excision  for rectal cancer: A retrospective study
Version: 1 Date: 14 Apr 2021
Reviewer:  Audrius Dulskas
Reviewer's report:
Dear Authors,
I want to congratulate you with this nice study. Still I have some comments and questions.
INTRODUCTION
-Da Vinci robot (Company name, City, Country)
METHODS
-How many patients were treated at your center during the study period
-what were the inclusion/exclusion criteria? - CONSORT flow chart should be added.
-More patients with ASA I were in R group compared to more patients with ASA III
-Why have you assessed only male urogenital function and none for female patients?
-Fig S1 - same structures with different names (IMA and IMV).
-Used questionnaires should be cited. Are they validated for the use in Chinese population?
RESULTS
-Why is the length of hospital stay so long? (9vs 12 days). In western countries it usually is 3-5
days. Is it because of the reimbursement programs?
-Risk of complications is also relatively high.
-What was the length of robotic docking time?
-What was the reason of conversion? What are the possible reasons of local recurrences? Who
did you define the local recurrence?
DISCUSSION
-First sentence - what do you mean by peripheral l/n?
-The discussion should start with you results.
-How can ileostomy decrease the anastomotic line bleeding?
-The prevention of anastomotic leak with ileostomy is also questionable and still discussed.
-On the whole - English should be improved. Avoid spoken English usage (What's, etc)
-safety and feasibility should be defined in the methods
The crucial limitations are small sample size
Review for 10.1186/s12876-021-01834-1 (2021)

Title: Comparison of the operative outcomes and learning curves between laparoscopic and
“Micro Hand S” robot-assisted total mesorectal excision  for rectal cancer: A retrospective study
Version: 4 Date: 25 May 2021
Reviewer:  Audrius Dulskas
Reviewer's report:
Dear Authors,
Thank you for the comments. The manuscripts improved a lot.
Review for 10.1186/s12876-021-01834-1 (2021)

Title: Comparison of the operative outcomes and learning curves between laparoscopic and
“Micro Hand S” robot-assisted total mesorectal excision  for rectal cancer: A retrospective study
Version: 4 Date: 30 May 2021
Reviewer's report:
Thanks for addressing all the reviewers’ comments. Good work.
As a minor correction, in the Methods, the total number of patients undergoing TME surgery
(206) added as the reviewer pointed out must be added to the results section, not in the methods.
Review for 10.1186/s12876-021-01830-5 (2021)

Title: Creatinine-lactate score predicts mortality in non-acetaminophen-induced acute liver
failure in patients listed for liver transplantation
Version: 2 Date: 18 Apr 2021
Reviewer's report:
Well, there are several issues, which could be addressed to improve the manuscript:
1. Lactate as a predictor is already described several times:
a. Bernal et al 2002 (The Lancet) and 2010 (J Hepatol 2010)
b. McQuillan et al. Liver Transpl 2005
c.Hadem et al. Clin Gastroenterol Hepatol 2008
The cut-off value for creatinine is fixed at 87.52 µmol/l. This is the normal value for creatinine.
How can this be predictive? Concern lactate level is given in table 1 with ng/dl. I never
recognized this kind of value, I know mg/dl or mmol/l. PLease correct it.
An increased lactate level together with poor kidney function in ALF is always a predictor for
worse outcome. The question is. can you speculate from your data, for which patients was the
transplant futile?? That is important.
Review for 10.1186/s12876-021-01830-5 (2021)

Title: Creatinine-lactate score predicts mortality in non-acetaminophen-induced acute liver
failure in patients listed for liver transplantation
Version: 3 Date: 11 May 2021
Reviewer's report:
The authors addressed all raised issue, but I am still a concern, which novelty these data may
provide for better understanding.
Review for 10.1186/s12876-021-01828-z (2021)

Title: Changing Trends in Liver Transplantation Indications in Saudi Arabia: From Hepatitis C
Virus Infection to Nonalcoholic Fatty Liver Disease
Version: 2 Date: 07 Mar 2021
Reviewer:  Nikoletta Tagkou
Reviewer's report:
This is an interesting single-center retrospective study that aimed to analyze trends in LT
indications in Saudi Arabia over a certain period of time. Overall, it is a very well designed
and executed study that utilizes the appropriate methodology in order to address the research
questions. The Introduction clearly summarizes the state of research in the field as well as the aim
and relevance of the study. The methods are presented in a clear manner and statistical analysis of
the data is technically sound. Furthermore, all the data are accessible and appropriately displayed
in the tables and figures. Finally, the Discussion, although long, thoroughly discusses the results
of the study in the context of recent literature. The fact that the authors recognize the limitations
and strengths of their research in the last paragraph is also endorsed.
Review for 10.1186/s12876-021-01828-z (2021)

Title: Changing Trends in Liver Transplantation Indications in Saudi Arabia: From Hepatitis C
Virus Infection to Nonalcoholic Fatty Liver Disease
Version: 2 Date: 03 Apr 2021
Reviewer's report:
GENERAL COMMENT
The Authors performed an original, timely and interesting study on trends in Liver
Transplantation Indications in Saudi Arabia showing that NAFLD has eclipsed HCV as main
indication. This is an hot topic. Some comments maybe raised at improving the quality of the
manuscript.
SPECIFIC COMMENTS
Literature about NAFLD should be updated. The strong bidirectional relationship with metabolic
comorbidities and the risk of cardiovascular disease morbidity and mortality should be
stressed. NAFLD and its severity (steatosis grade/fibrosis severity) have been associated with
cardiovascular risk. A growing mole of patients will with advanced NAFLD and cardiometabolic
disease will be observed. Moreover, a sexual dimorphism has been recently recognized in
NAFLD.
Based on these premises, we agree with the Authors that an active policy finding of NAFLD in
high risk-individuals should be advoked to better allocate resources.
Suggested updated literature:
Lonardo A, Int J Mol Sci. 2020;21:5888.
Cotter TG, Gastroenterology 2020;158:1851-1864.
Targher G, J Hepatol. 2016;65:589-600.
Cai J, Circ Res. 2020;126:679–704
Ballestri S, Diagnostics (Basel) 2021;11:98.
Lonardo A, Hepatology. 2019;70:1457-1469.
Noureddin M, Gastroenterology 2020;159:1985-1987.e4.
Review for 10.1186/s12876-021-01828-z (2021)

Title: Changing Trends in Liver Transplantation Indications in Saudi Arabia: From Hepatitis C
Virus Infection to Nonalcoholic Fatty Liver Disease
Version: 4 Date: 30 Apr 2021
Reviewer's report:
The Authors addressed all the reviewers' comments. The manuscript has substantially improved.
Review for 10.1186/s12876-021-01828-z (2021)

Title: Changing Trends in Liver Transplantation Indications in Saudi Arabia: From Hepatitis C
Virus Infection to Nonalcoholic Fatty Liver Disease
Version: 4 Date: 13 May 2021
Reviewer:  Nikoletta Tagkou
Reviewer's report:
We thank the authors for thoroughly considering and replying to our comments, point by
point. As advised by the fellow Reviewer, recent literature about NAFLD is now added to the
manuscript, improving its quality and relevance. A minor revision is now suggested only to
correct some errors that can be found in the following lines:
1. line 78, "was the most common indications" kindly rephrase
2. line 116, "the availability of DAAs ... to effectively treat" kindly rephrase
3. line 121, "single-center in SA" words "retrospective study" missing
4. line 208, similarly to point 3.
Review for 10.1186/s12876-021-01828-z (2021)

Title: Changing Trends in Liver Transplantation Indications in Saudi Arabia: From Hepatitis C
Virus Infection to Nonalcoholic Fatty Liver Disease
Version: 5 Date: 22 May 2021
Reviewer:  Nikoletta Tagkou
Reviewer's report:
The Authors addressed all the reviewers' comments.
No further revision is necessary before publication.
Review for 10.1186/s12876-021-01836-z (2021)

Title: Biopsy in emergency gastroscopy does not increase the risk of rebleeding in patients with
Forrest I acute nonvariceal upper gastrointestinal bleeding combined with suspected malignant
gastric ulcer: a multicenter retrospective cohort study
Version: 3 Date: 27 Feb 2021
Reviewer's report:
This manuscript described the usefulness of biopsies during EG in patients with Forrest I
ANUGIB combined with SMGU using a propensity-matched approach, and demonstrated
that there were no significant differences in the risk of rebleeding in patients with Forrest I
ANVUGIB combined with SMGU during EG between biopsy and no-biopsy groups. This paper
is an interesting work. My comments were as follows:
1. I agree the result that there were no significant differences in the risk of rebleeding in patients
with Forrest I ANVUGIB combined with SMGU during EG between biopsy and no-biopsy
groups in clinical practice. However, the authors should add the data about the endoscopic
hemostatic therapy during emergency endoscopy in Table 1 because it might be associated with
rebleeding.
2. Rebleeding was defined when a significant drop in hemoglobin was observed. How much
hemoglobin decrease does a significant drop mean?
3. About Figure 2.
I think “30-day survival” should be changed to “30-day survival without rebleeding” or
“rebleeding-free 30-day survival”.
4. RWS and EVB should be excluded from abbreviation lists because they were written only
once in the text.
5. There is mistake in percentage of patients who underwent biopsy in Figure 1.
Wrong 401 (39.0%)   Correct 401 (39.7%)
Review for 10.1186/s12876-021-01836-z (2021)

Title: Biopsy in emergency gastroscopy does not increase the risk of rebleeding in patients with
Forrest I acute nonvariceal upper gastrointestinal bleeding combined with suspected malignant
gastric ulcer: a multicenter retrospective cohort study
Version: 3 Date: 30 Apr 2021
Reviewer's report:
Review on the paper by Quchuan Zhao and Tianyu Chi.
In this paper authors used a propensity score matching to compare the risk of rebleeding and the
cost in patients presenting with Forest 1 gastric ulcer of suspected malignant origin according
to the realization of biopsies.
They suggest that there is no increased risk of bleeding and no cost increase.
I must say that I am quite confuse with the structure of the paper.
Indeed it is quite unusual to have rebleeding as primary outcome and cost as secondary. Nothing
ius told about the cost analysis so validity of results presented cannot be ascertained.
The matching procedure should have been more detailed.
Same is for the rebleeding ascertainment, what if the definition of “vital sign instability
and a significant drop in hemoglobin”. Nothing is told about threshold value, or if authors
reconstructed rebleeding cases based on individual patient’s data analysis (Hb or blood pressure
values) or just based on hospital reports.
If rebleeding was not just based on a specific code, I hope the occurrence of the event was
assessed blinded to the knowledge that a biopsy was performed or not.
Some of the results presented on table one are contra intuitive, for example the higher proportion
of patients on clopidogrel in the biopsy versus non biopsy group both before (17% vs 6.6%) and
after matching (18.5% vs 13.9%). Same is true for size of the ulcer, higher proportion of small
ulcers in the non-biopsy than in the biopsy group.
Even if statistical significance is not reached is seems surprising that point estimates for
rebleeding are lower in ASA and clopidogrel users than in non-users
It would have been of interest to give explanation on the reasons associated with biopsies being
performed or not.
I don't really understand how pathology results can be provided in the group of patients who
did not have biopsies.
The first two paragraphs of the discussion are more appropriate, and the beginning of the third
one belongs to the method section
Review for 10.1186/s12876-021-01836-z (2021)

Title: Biopsy in emergency gastroscopy does not increase the risk of rebleeding in patients with
Forrest I acute nonvariceal upper gastrointestinal bleeding combined with suspected malignant
gastric ulcer: a multicenter retrospective cohort study
Version: 3 Date: 01 May 2021
Reviewer's report:
interesting and well written work.
Review for 10.1186/s12876-021-01836-z (2021)

Title: Biopsy in emergency gastroscopy does not increase the risk of rebleeding in patients with
Forrest I acute nonvariceal upper gastrointestinal bleeding combined with suspected malignant
gastric ulcer: a multicenter retrospective cohort study
Version: 4 Date: 13 May 2021
Reviewer's report:
The authors have replied to all questions raised by me.
I think this manuscript reached to be accepted.
Review for 10.1186/s12876-021-01836-z (2021)

Title: Biopsy in emergency gastroscopy does not increase the risk of rebleeding in patients with
Forrest I acute nonvariceal upper gastrointestinal bleeding combined with suspected malignant
gastric ulcer: a multicenter retrospective cohort study
Version: 4 Date: 30 May 2021
Reviewer's report:
Interesting work
Review for 10.1186/s12876-021-01835-0 (2021)

Title: Pediatric living-donor liver transplantation using right posterior segment grafts
Version: 4 Date: 27 May 2021
Reviewer:  Allan M Concejero
Reviewer's report:
The queries and questions to the authors have been adequately addressed in the revised
manuscript. This is a good reference material for larger children in pediatric LDLT. The surgical
pitfalls and indications to use the right posterior segment have been pointed out.
Review for 10.1186/s12876-021-01831-4 (2021)

Title: Clinicopathological characteristics and prognosis of signet ring cell carcinoma of the
gallbladder
Version: 0 Date: 18 Apr 2021
Reviewer's report:
The manuscript by Wang and colleagues entitled " Clinicopathological characteristics and
prognosis of signet ring cell carcinoma of the gallbladder" is well written and organized.
However, multiple issues need to be addressed prior to further consideration.
Major issues:
• The 8th edition of AJCC TNM staging system should be applied in this study instead of the
7th edition..
•
• In table 3, the baseline information of each group should be listed and analyzed.
•
Minor issues:
1. The English should be polished by a native speaker.
Review for 10.1186/s12876-021-01831-4 (2021)

Title: Clinicopathological characteristics and prognosis of signet ring cell carcinoma of the
gallbladder
Version: 0 Date: 20 Apr 2021
Reviewer:  Feng Wei
Reviewer's report:
The authors described the clinicopathologic features and prognosis of SRC had potential clinical
value in gallbladder adenocarcinoma.
The design of the study is reasonable, however some of the details remain problematic. I have
more comments regarding the study.
1] In figure 1, 2,364 whose diagnosis confirmation # positive histology and 2,549 whose tumor
sequence number were excluded from the study. Why these patients are excluded and it needs
to be explained in the research method or discussion section at least.
2] Overall survival [OS] of SRC of gallbladder was showed in this study. Cancer-specific
survival [CSS] is another prognostic parameter and is a useful complement to OS. Can authors
add CSS data in this study?
3] In study, 22,781 gallbladder adenocarcinomas retrieved, 377 (1.7%) were SRC and the other
22,404 were non-SRC. The baseline of 377 SRC patients (e.g. age, sex, tumor size, etc.),
however, was different from the no-SRC. Selection bias  maybe occur in the study. propensity
score matching (PSM) can reduce the effect of selection bias in studies. Can authors add PSM
data in this study?
4] In tables 2 and 3, what do you mean“Reference ”? Please add its meaning selection bias is
prevalent in retrospective studies.
5] The SEER dataset does not cover many covariates, such as comorbidities, which would greatly
impact survival. This part should be discussed as source of bias in the discussion section.
6] Language needs polishing. Preferably use a professional editing service and provide a
certificate.
Review for 10.1186/s12876-021-01831-4 (2021)

Title: Clinicopathological characteristics and prognosis of signet ring cell carcinoma of the
gallbladder
Version: 1 Date: 24 May 2021
Reviewer:  Feng Wei
Reviewer's report:
In the previous review proposal, I suggested that the authors add propensity score matching
(PSM). The authors have added the PSM data in the revised manuscript. Here is a small problem
that the CS analysis of Figure 2A in the revision is consistent with Figure 2 in the first manuscript.
Is the CS analysis result in Figure 2 based on before or after PSM?
Review for 10.1186/s12876-021-01829-y (2021)

Title: Three-dimensional visualization improves the endoscopic diagnosis of superficial gastric
neoplasia
Version: 1 Date: 09 Feb 2021
Reviewer's report:
In this article, Higuchi et al. explorated the usefulness of 3D images in delineation and
determining the morphology for early gastric cancers.  I think this topic is very interesting and
clinically important because early gastric cancer is difficult to be detected in routine endoscopy
exam. It might provide another opportunity toward better diagnosis with this technology.
However, I have several questions:
1.In the WLI group, do you have indigocarmine spray? In the conventional 2D observation, it
is difficult to delineate, and determine the morphology without chromoendoscopy. I think it is
more meaningful to compare the efficacy in the presence of chromoendoscopy.
2.Have you compared the group A and group B (differed by the chronology of 2D/3D images)
for the difference? Since it a cross-over study, it may be important to see if different study
protocol would have influenced the outcomes.
3.How do you determine the "correct" morphology of the lesions in this study? The morphologic
classification systems such as Paris classification are notorious for discrepancy in determine the
flat/depressed lesions even among experts. This is also true in this study that the flat/depressed
lesions have suboptimal accuracy with the aids of 3D image and NBI. I do believe 3D image
can be more accurate in morphology, but the question need to be answered for the validity of
this analysis.
Review for 10.1186/s12876-021-01829-y (2021)

Title: Three-dimensional visualization improves the endoscopic diagnosis of superficial gastric
neoplasia
Version: 1 Date: 12 Feb 2021
Reviewer's report:
Thank you for your efforts on research and innovation of endoscopic field.
This study provides us a new vision of future on concepts, study design and advances in
technology. I would recommend to accept your article if some details could be clarified after
your revision.
Please show us the process of how participants evaluate tumor under 3D visualization and then
drew an endoscopically assumed tumor margin on a 2D colon print.
Please show us how you could make sure there is no deviation or error when the participants
evaluate tumor extent under 3D condition and then drew a margin on a 2D image color print.
Thank you all. I am looking forward for your revision.
Review for 10.1186/s12876-021-01829-y (2021)

Title: Three-dimensional visualization improves the endoscopic diagnosis of superficial gastric
neoplasia
Version: 3 Date: 22 Apr 2021
Reviewer's report:
Thank you for your efforts. All of you did a great job to improving the diagnostic accuracy
which leading to the excellence of endoscopic treatment. We are looking forward for your further
progression of new research associating with 3D technology.
Review for 10.1186/s12876-021-01827-0 (2021)

Title: Selective inhibition of soluble TNF using XPro1595 relieves pain and attenuates cerulein-
induced pathology in mice
Version: 3 Date: 09 Mar 2021
Reviewer:  Mustafa Kaplan
Reviewer's report:
Dear Editor,
I would like to express that I find the subject and method of study very good.
However, it is very important to make some corrections in terms of method regarding the writing.
If these issues are summarized;
1. It is seen that the abstract part of the article is rather irregular and insufficient. It should be
shortened and edited in accordance with the writing principles. The method part is not mentioned
at all in the abstract part. Also, in the abstract part, the background part should not be that long. In
addition, the abstract should include the outline of the article and should not contain unnecessary
information.
2. The introduction of the article is quite long and needs to be shortened.
3. The approval obtained from the ethics committee for experimental animals should be given
in detail.
4. In the methodology part of the article, detailed information about the methodology should be
given, such as how many groups the experimental animals are divided into.
5. Is there validity of the pancreatitis scoring used in the article? Detailed information should
be given about where it was taken from.
6. In the results part of the article, rather than giving the discussion obtained from the rats, the
efficacy of the relevant substance used was mentioned.
7. Detailed descriptions of how useful Xpro1595 is. Most of the information given in the result
should perhaps be given in the discussion section.
8. When the result part is this long, of course the discussion part was also just as short. However,
the discussion section should be longer.
9. As a study of experimental animals, although the subject is quite interesting, beautiful and
well written, its methodology is unfortunately poorly written.
10. As a result, if the desired corrections are made, the article must be accepted for publication.
Sincerly.
Review for 10.1186/s12876-021-01827-0 (2021)

Title: Selective inhibition of soluble TNF using XPro1595 relieves pain and attenuates cerulein-
induced pathology in mice
Version: 3 Date: 28 Mar 2021
Reviewer's report:
The study is well designed in.The claims have proved that selectively inhibiting solTNF using
XPro1595 improved the pathophysiological and neurological sequelae of cerulein-induced
pancreatitis in mice. This study demonstrates that XPro1595 may be useful in relieving the
inflammation and pain of acute pancreatitis.The statistical methods used in this study are
correct.The results of the study were in line with the expectations of our research team.This
study is somewhat innovative and there are no similar studies available.There are of course some
limitations to the study and the effect of XPro1595 injection on changes in the expression of the
various isoforms of TNF# caused by acute pancreatitis should be tested.
Review for 10.1186/s12876-021-01827-0 (2021)

Title: Selective inhibition of soluble TNF using XPro1595 relieves pain and attenuates cerulein-
induced pathology in mice
Version: 4 Date: 12 Apr 2021
Reviewer:  Mustafa Kaplan
Reviewer's report:
Dear Authors,
I would like to express that I find the subject and method of study very good. As a study of
experimental animals, although the subject is quite interesting, beautiful and well written. The
article could be accepted for publication.
Sincerly.
Review for 10.1186/s12876-021-01824-3 (2021)

Title: Waist-to-height ratio and non-alcoholic fatty liver disease in adults
Version: 1 Date: 05 Mar 2021
Reviewer's report:
I read with interest the manuscript of Sheng et al. regarding the relationship between Waist-to-
height ratio and NAFLD on ultrasonography in 14,125 participants from a health examination
programme. In this cross-sectional study the authors found that WHtR is associated with an
increased prevalence of NAFLD.
The topic is not so novel indeed, as convincing evidence indicates that waist-to-height
ratio (WHtR) is associated with central obesity, diabetes, hypertension, metabolic syndrome
and,consequently, NAFLD. This study adds new data on this topic. I have however some
concerns:
- through the manuscript the authors used the terms “incidence”, however it is a cross-sectional
study in which the time variable is not present. Importantly, they have to use “prevalence”.
- Table 3, I have not understood the part regarding WHtR ratio (Quintile, per SD increase).
Since WHtR ratio is treated as categorical variable, what does  “per SD increase” mean in
this case? In addition, I think that there are an over adjustment in the models, as authors have
included WHtR ratio as independent variable but also height, BMI, AST, ALT, GGT. Odds
ratio as markedly higher, especially in model 1 and 2. I did not understand the reason. Are there
important collinearity in the models? Are there non-normally distribuited variables that need
to be logarithmically transformed? Since figure 1 shows a non-linear association between the
WHtR and NAFLD, I am not sure that a logistic regression model is the best way. Probably,
other regression models are more appropriate.