JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02228-7 (2022)

Title: CD63-positive extracellular vesicles are potential diagnostic biomarkers of pancreatic
ductal adenocarcinoma
Version: 2 Date: 24 Nov 2021
Reviewer:  Mohamed M. Zaid
Reviewer's report:
This manuscript investigates the utility of EVs in the early detection of pancreatic ductal
adenocarcinoma. The authors tested their hypothesis on three retrospective cohorts, and the
results supported the utilization of EVs in combination with CA-19 for the early detection
purposes.
I have few minor comments and questions for the authors:
-The nomenclature is not consistent, sometimes you refer to the healthy controls as healthy
donors, and my understanding is that they are the same thing.
-The used cohorts are really small in number, did you do power calculation to determine if the
numbers sufficient for this power and alpha?
-In the method section you referred to the healthy donors as patients, which is not true. Right?
-What is the chemo/radiotherapy statuses for these patients? Did they receive neoadjuvant or
adjuvant therapy? How does that impact the quantification of the EVs?
-It would be interesting to show if the  EVs can also detect the recurrence
-Do you think imaging can play a complementary role to the EVs and CA-19?
Review for 10.1186/s12876-022-02228-7 (2022)

Title: CD63-positive extracellular vesicles are potential diagnostic biomarkers of pancreatic
ductal adenocarcinoma
Version: 2 Date: 02 Dec 2021
Reviewer's report:
In this Manuscript, Odaka et.al. reported the quantitative measurement of serum level CD63+
EVs and platelet derived EVs (CD41+and CD61+) in PDAC patients and healthy controls and
evaluated their potential use as biomarkers for PDAC.
This is an interesting study however the analyses have been done using small cohorts.
Specifically, the small number of PDAC patients in the cohort 2 and cohort 3 are likely to limit
analysis necessary to reach conclusions from the observed changes. Overall, to further strengthen
the manuscript, authors need to address some comments herein.
Comments:
1. It is important to determine the purities of the EVs in general. In the manuscript, patient serum-
and platelet-derived EV characterizations have not been done to detect their morphology and
sizes by transmission electron microscopy and by nano sight analysis respectively.
2. Authors described in the text as ‘universal CD63+ EVs’. EVs carrying tetraspanin CD9 or
CD81 form in the endosome but not CD63. Therefore, ‘universal EV’s are those which carries
CD63 together with at least one other tetraspanin (CD9 or CD81) that may represent to endosome
derived EVs (PMID: 26858453). Did authors detect other EV-associated tetraspanins e.g, CD9
or CD81 in the patient serum? It is suggested that either remove the ‘universal’ word from the
text or screen for another tetraspanin in addition to CD63.
3. In the result section page 13, line 154, authors described the combinational use of CD63+EVs
and CA19-9 as there were low correlation coefficient between the two. According to the
description in the method section, the detection assays of CD63+EVs and CA19-9 were
different. Therefore, it is unclear that how the values were combined and what was the rationale
behind it. Authors should explain that in details.
4. Authors examined the tumor burden on the serum levels EVs in two cohorts after surgery.
The number of the patients were too few to draw a strong conclusion that universal and platelet
derived EVs ‘reflect the tumor burden before and after surgery’.
Additional examples are necessary.
5. Page 13, line 151: Please correct the value from 0.853 to 0.858
6. Fig. 1: Y-axes of a, b and c should be in the same scale.
7. Fig. 4: Y-axes of b, c and d should be in the same scale.
Review for 10.1186/s12876-022-02228-7 (2022)

Title: CD63-positive extracellular vesicles are potential diagnostic biomarkers of pancreatic
ductal adenocarcinoma
Version: 5 Date: 16 Mar 2022
Reviewer:  Mohamed M. Zaid
Reviewer's report:
I'd like to thank the authors for addressing my  comments and answering  the questions.
I have no further concerns.
Review for 10.1186/s12876-022-02213-0 (2022)

Title: Corticosteroid suppresses urea-cycle-related gene expressions in ornithine
transcarbamylase deficiency
Version: 4 Date: 22 Jan 2022
Reviewer's report:
The author adequately responded to the questions raised by the reviewer in the first draft.
The reviewer thinks the authors are requested to answer one more question before this  paper
is published in BMC Gastroenterology.
The author states “ARG1 mRNA expression level in Otcspf-ash mice may have been decreased
as compensation for the decrease of ornithine level” (p16, lines 13-15).
OTCD patients generally need a higher ornithine concentration than healthy individuals to
maximize limited citrulline synthesis. For this reason, it seems to the reviewer that OTCD
individuals (both human and mouse) are expected to have high ARG1 activity to supply enough
ornithine.
Review for 10.1186/s12876-022-02213-0 (2022)

Title: Corticosteroid suppresses urea-cycle-related gene expressions in ornithine
transcarbamylase deficiency
Version: 7 Date: 10 Mar 2022
Reviewer's report:
BMC Gastroenterology   Imoto K paper                  01222022
The author adequately responded to the questions raised by the reviewer in the first draft.
The reviewer thinks the authors are requested to answer one more question before this  paper
is published in BMC Gastroenterology.
The author states “ARG1 mRNA expression level in Otcspf-ash mice may have been decreased
as compensation for the decrease of ornithine level” (p16, lines 13-15).
OTCD patients generally need a higher ornithine concentration than healthy individuals to
maximize limited citrulline synthesis. For this reason, it seems to the reviewer that OTCD
individuals (both human and mouse) are expected to have high ARG1 activity to supply enough
ornithine.
The reviewer thinks that to thoroughly elucidate effect of corticosteroid hormone on ureagenesis,
some more extended studies employing metabolomic, proteomic and molecular genetic
techniques is necessary. In this regard, the present article does not contain the whole information
that is necessary to address the research question in detail. Nonetheless, the reviewer supports
that this report can be published because  the reviewer believes that this work is the first part
that is essential for further extended research.  The reviewer  expects to  read further studies.
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 2 Date: 15 Dec 2021
Reviewer:  Kuen-chang Hsieh
Reviewer's report:
Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients
This study compared the diagnosis of sarcopenia patients with CT, BIA and grip strength in
cirrhotic patients. The research topic has clinical significance. There are still some problems
in the manuscript. It is recommended that the authors clarify them in order to increase the
readability and completeness of this research.
Please provide the approved IRB number.
On page 8, the authors have stated that "the calculation of the abdominal muscle cross-section
was performed by Matlab". I personally think it should be the software developed by the authors
themselves. But how to determine that the software can correctly calculate the muscle area of
the cross-section, the authors need to explain it.
In Table 1, the average age of without sarcopenia is 58, 63, respectively. Why is the total average
value 63? There should be a problem, please confirm with the authors.
In this study, the cross-sectional area muscle mass obtained by CT was used as the comparison
standard for the study, and it is called the gold standard. Why? For the authors should cite the
literature [7]. What is the difference between the reference value of CT and other existing judging
sarcopenia indicators? Please clarify it.
On the seventh page, in the measurement section of BIA, there were two indicators, SMI and
ASM. SMI is skeletal muscle index, ASM is appendicular skeletal muscle. But in the description
of this paragraph, it was mentioned that "The SMI cut-off by BIA for the diagnosis of sarcopenia
was based on the JSH criteria...". I think the "SMI" should be "ASM". please confirm.
Page 10, Line 1, "CT was 43 and 31 cm2/m2," The correct label should be "cm2/m2". Many
of the superscripts in the manuscript were not used correctly, and it is recommended to correct
them.
Why was the height of the abdominal muscle cross-section obtained from the CT scan L3. Please
indicate the source of the reference.
The description of the preparation conditions for BIA measurement was too few, please add it.
Correlation coefficient (R) is recommended to be written as r in order to distinguish it from
resistance (R).
Although the correlation between MC780 and CT presented in the manuscript was not
good, whether it can support the conclusion "Nonetheless, for the BIA, the current cut-off
demonstrated unacceptable sensitivity to detect sarcopenia.", the authors should be reconsider.
The correlation between HSG and CT was not good. Why was there such a big difference in
the evaluation results of BIA and HSG, which are commonly used to judge sarcopenic? Please
add an explanation to discuss it.
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 2 Date: 15 Dec 2021
Reviewer:  Hsueh-kuan Lu
Reviewer's report:
In this study, "Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA)
in the diagnosis of sarcopenia in cirrhotic patients", the authors compared CT, BIA and the
diagnosis of cirrhotic patients with sarcopenia. The topic is very interesting. However, there
seems to be some doubts about the "recruitment exclusion conditions", the authors are requested
to confirm and explain.
First, in the summary statement "The HGS was strongly correlated with skeleton muscle
index (SMI) by CT (r=0.81, p<0.001) and had an excellent diagnostic performance for
detecting sarcopenia by using JSH criteria the sensitivity, specificity, NPV and PPV were
88.2%,100%,100%, and 98.7% respectively. In contrast, only 2 of 30 patients (6.7%) met
sarcopenic criteria by BIA. Among sarcopenic patients, the result showed a fair correlation
between SMI and BIA (r2 = 0.54; P<0.002)”.
Why used "r" for the former and "r2" for the latter? Furthermore, why did the statistics of “only
2 of 30 patients (6.7%) met sarcopenic criteria by BIA” reach the level of “P<0.002” and have
the conclusion of "fair correlation"? Please confirm it by the authors.
BIA can predict sarcopenia. It does not mean that BIA can predict sarcopenia in unhealthy
people with uneven body water distribution. May I ask the authors, what is the principle of
using BIA to assess body composition, including muscle mass? What are the limiting factors
for measurement?
Any edema or ascites will affect the accuracy and validity of the BIA measurement. Why
the exclusion clause adopted by the authors is "Ascites grade >2 by International Ascites
Club grading system"? Why was the subjects recruited in this study selected for the restricted
population of BIA instruments? The authors are requested to confirm and explain them.
The study recruited restricted populations measured by BIA instruments. Perhaps, the
predictable presentation of the "conclusion" was of course "inaccurate."
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 3 Date: 19 Jan 2022
Reviewer:  Hsueh-kuan Lu
Reviewer's report:
The authors responded: "We did agree BIA might not predict sarcopenia in unhealthy people
especially when patients were in the state of fluid retention which led to the exclusion criteria of
more than grade 2 ascites in this study. " Why the exclusion clause adopted by the authors was
"Ascites grade >2 by International Ascites Club grading system"? In other words, why were the
authors screening (recruiting) subjects not "Ascites grade >1" or "Ascites grade >3"? Is there any
reference or basis to support the selection? Was the condition "Ascites grade >2" appropriate?
The authors have added "We added term cirrhosis without significant ascites to the conclusion
of the study." to the revised manuscript. How was "without significant ascites" diagnosed? Or
was it subjectively determined by the authors?
If the authors were unable to demonstrate that "the study has recruited subjects who did not
belong to the exclusion group of the BIA instrument," perhaps, the predictable presentation
of the "conclusion" was of course "inaccurate." And that, this research will not be able to see
specific contributions and highlights. If the above can be proved, this research will have a certain
degree of contribution.
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 3 Date: 24 Jan 2022
Reviewer:  Kuen-chang Hsieh
Reviewer's report:
Thank you to the author for carefully replying or revising the comments one by one. However,
there are still doubts, and I personally think that the authors need to strengthen supplementary
explanations.
In the study, the self-written "matlab" was used for L3/4 muscle calculation. This was a very
important key procedure for this study. Although the authors have "detailed" their process on
page 8, I still have doubts about the reliability and validity of this program or self-written
software. The author should supplement the description of the reliability and validity of this
software, not just by ICC and CI.
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 5 Date: 09 Mar 2022
Reviewer:  Hsueh-kuan Lu
Reviewer's report:
All explanations and replies are reasonable and sufficient.
Review for 10.1186/s12876-022-02236-7 (2022)

Title: Utility of handgrip strength (HGS) and bioelectrical impedance analysis (BIA) in the
diagnosis of sarcopenia in cirrhotic patients.
Version: 5 Date: 10 Mar 2022
Reviewer:  Kuen-chang Hsieh
Reviewer's report:
Thanks to the authors for the additional information. According to the authors' supplementary
information, the "semiautomatic software" used to calculate muscle mass in this study was
developed by Jae-Hoon Kim, et al. in Korea. It should be clearly stated in the manuscript
that this study used the software "Semi-automatic measurement tool (BMI CT ver 6.0)" to
measure muscle mass. Rather than using "Matlab" to develop. "Matlab" was just a development
environment. Authors are advised to correct information related to the manuscript.
Review for 10.1186/s12876-022-02223-y (2022)

Title: Effect of clinical vs. administrative data definitions on the epidemiology of C. difficile
among hospitalized individuals with IBD: A population-based cohort study
Version: 1 Date: 07 Dec 2021
Reviewer's report:
Shaffer-CDI in ICD codes vs lab tests
The authors have used linked datasets from Manitoba 2005-2014 to compare CDI rates among
hospitalized patients when CDI is classified based on discharge ICD-10 codes versus when CDI
is classified based on lab testing.  They looked at this question for patients with IBD (Crohn’s
and UC) and for matched controls without IBD.  They found that the ICD-10 codes were (to my
surprise) not bad at classifying CDI with a sensitivity of 70-80% and near perfect specificity.
The sensitivity was slightly worse among those with IBD than among the matched controls
without IBD, which also was surprising.  In general, this paper is professionally assembled and
it is a useful addition to those working in epidemiology related to CDI.  While not entirely novel,
it adds incrementally to their own prior work (reference 11) and that of others (e.g., ref 27).
My most important comment is related to their emphasis which often seems to wander away from
the question of interest (which is comparing CDI classified by ICD-10 codes vs CDI classified
by labs).  To be specific, take Table 1.  This table emphasizes the comparison of those with IBD
vs matched controls without IBD.  This is not the comparison of interest!  Rather, the columns
should be rearranged so that they are comparing risk factors when CDI is classified via ICD-10
vs when CDI is classified via labs.  E.g., 5-ASA use for CDI by ICD-10 vs 5-ASA use for CDI
by labs, etc.  They could do this first for IBD and then for non-IBD.  Elsewhere in the manuscript
similar changes of emphasis could be made and the manuscript would be improved.
Less important:
1. Discussion - Although the authors recognize the problem of CDI colonization in the
limitations section, they should further tone down their statement in the Discussion (end of
first page) about this, which diminishes this very important problem that plagues CDI research.
Although I agree that a positive C. diff is invariably treated in IBD patients, this doesn’t mean
that these are true CDI cases.  A large proportion of these patients are colonized and treating
C. diff makes no difference.  Ultimately, the true diagnosis of CDI is clinical and cannot be
ascertained retrospectively.
2. Methods - The final sentence before the “Study Measures” section implies that have linked
individual patients within the datasets—i.e., that each patient is a single row of data.  This is a
very important point and, assuming this is the case, it should be stated even more explicitly.  If
I somehow misunderstood and this is not the case, it’s a major problem.
3. The most recent data is from 2014 making the study data a minimum of 8 years old and a
maximum of 16 years old.  The fact that the data is relatively stale should be recognized as a
limitation.
Review for 10.1186/s12876-022-02223-y (2022)

Title: Effect of clinical vs. administrative data definitions on the epidemiology of C. difficile
among hospitalized individuals with IBD: A population-based cohort study
Version: 1 Date: 14 Dec 2021
Reviewer's report:
This is an interesting original article about the “Effect of clinical vs. administrative data
definitions on the epidemiology of C. difficile among hospitalized individuals with IBD: A
population-based cohort study „
There are some formal requirements that need to be corrected:
1. There are a few typo, please revise and correct them.
2. Please check the reference rules and correct them accordingly.
3. Please use the official format the journal requested in the abstract:
Background, Methods, Results, Conclusions
I have a few points according to the article:
1. Please consider to relocate the last sentence of the introduction to the methods.
2. Please help me clear what was the matching system.
• on page 8th and 10th:  “Cases of IBD in the UMIBDED, (as of March 2015, n=8,277), are
matched 1:10 to age, sex and area of residence (at time of IBD diagnosis) matched controls
(n=72,387).” „The UMIBDED (April 1, 1984 – March 31, 2014) was used to identify individuals
with IBD, who were matched 1: 10 to those without IBD on age, sex, and area of residence (at
IBD diagnosis/ index date).”
• on page 10th: “Each individual with IBD with CDI diagnosis during a hospitalization was
matched with four IBD cases without a hospital record of CDI on or prior to the CDI index date
(hospital admission date for first hospitalization with CDI), according to IBD type (UC vs. CD),
gender, year of IBD diagnosis, and age.“
Why is it relevant in this study how in the UMIBDED database are the patients matched with
non-IBD patients?
3. on the page 12: “and a non-statistically significant decrease based on the DAD (APC=-4.7%,
95% CI -10.6, 1.7, P=0.12).”  - It would be better to say statistically non-significant but strong
tendency of decreasing…
4. Im suggesting to use the supplementary figure 1 as one of the main figure.
5. Is there a data about the concordance between the 108 lab and the 110 DAD patient? Were
they the same patients?
6. the discussion is too long
Review for 10.1186/s12876-022-02223-y (2022)

Title: Effect of clinical vs. administrative data definitions on the epidemiology of C. difficile
among hospitalized individuals with IBD: A population-based cohort study
Version: 2 Date: 22 Feb 2022
Reviewer's report:
Although I continue to feel that the paper's emphasis is at times misplaced, my comments have
been adequately addressed.
Review for 10.1186/s12876-022-02235-8 (2022)

Title: Clinical Characteristics and Treatment Outcomes of Primary Malignant Melanoma of
Esophagus: A Single Center Experience
Version: 1 Date: 23 Dec 2021
Reviewer's report:
Very interesting paper with novel conclusion. But due to the limited number and retrospective
research, it is difficult to give a definite conclusion as surgery did not significantly improve
overall survival. More cases and data need to be added in to research, such as margin of
surgery#gene mutation and TMB.
More basic research should be added to further explore relevant mechanisms.
Review for 10.1186/s12876-022-02235-8 (2022)

Title: Clinical Characteristics and Treatment Outcomes of Primary Malignant Melanoma of
Esophagus: A Single Center Experience
Version: 1 Date: 24 Dec 2021
Reviewer's report:
I reviewed the manuscript regarding mucosal melanoma of esophagus with certain interests.
Although the number of the patients in the present study was small, I think it is worth being
recorded considering its rarity. I have particular interests in two topics; one is a clinical impact
of immune-checkpoint inhibitors for PMME, and the other is the prognostic factors of PMME.
The followings are my minor comments.
1. Please consider adding Kaplan-Meier curves between those who received immune-checkpoint
inhibitors (regardless of adjuvant or metastatic setting) and those who did not.
2. There are only a few articles regarding immune-checkpoint inhibitors for PMME, but
several studies of mucosal melanoma including PMME have been published. Please update
the references by adding recent articles regarding immune-checkpoint inhibitors for mucosal
melanoma.
3. You demonstrated tumor morphology of mass-forming / infiltrative can be a prognostic factor
of PMME. This may be attributed to the tumor thickness, which is a main component of T
category in cutaneous melanoma. Please add the tumor morphology status (mass-forming /
infiltrative) in Table 2 and 3, and if possible, consider adding tumor thickness in addition to
tumor size.
4. In Figure 2B to D, please add the number of the patients in each cohort.
5. In Figure 2C, please consider dividing ‘N+ or M1’ cohort into each ‘N+’ or ‘M1’ cohort.
6. If available, please add BRAF and PD-L1 status.
Review for 10.1186/s12876-022-02235-8 (2022)

Title: Clinical Characteristics and Treatment Outcomes of Primary Malignant Melanoma of
Esophagus: A Single Center Experience
Version: 3 Date: 26 Feb 2022
Reviewer's report:
The authors have done a good job of addressing my and the other reviewers' comments. I have
no more other comments.
Review for 10.1186/s12876-022-02235-8 (2022)

Title: Clinical Characteristics and Treatment Outcomes of Primary Malignant Melanoma of
Esophagus: A Single Center Experience
Version: 3 Date: 02 Mar 2022
Reviewer's report:
“Clinical Characteristics and Treatment Outcomes of Primary Malignant Melanoma of
Esophagus: A Single Center Experience” retrospectively reviewed 17 patients diagnosed with
PMME. This manuscript has a depth analysis for PMME and interesting discovery ,but dure to
limited case number, the conclusions need to be very carefully.
As#surgery did not significantly improve overall survival while patients with diffusely
infiltrative tumor morphology(only two cases) showed better overall survival.
And please also mention the sample size and statistical differences during the discussion.
Review for 10.1186/s12876-022-02216-x (2022)

Title: Remnant cholesterol/high-density lipoprotein cholesterol ratio is a new powerful tool for
identifying non-alcoholic fatty liver disease
Version: 2 Date: 02 Jan 2022
Reviewer's report:
This is an interesting cross-sectional study on the role of remnant cholesterol/high-density
lipoprotein cholesterol ratio and NAFLD in a large serie of adult subjects screened for NAFLD
by abdominal ultrasound. The Authors conclude that (RC/ HDL-C) ratio may be a new powerful
tool for identifying non-alcoholic fatty liver disease.
However, patient’s selection (excluding those with impaired fasting glucose and/or diabetes and
those taking oral medications at baseline) may have ended to an atypical low/normal weight
NAFLD population. In fact, most NAFLD patients are overweight/obese, have diabetes and the
metabolic syndrome and therefore most of them are under polytherapy. In my opinion, these
selection bias can cause interpretation problems and indicate conclusions that are difficult to
extend to the large number of subjects with NAFLD. Therefore, it would be more correct from
a methodological point of view to consider the whole population of subjects with NAFLD and
to analyze diabetes and drug therapies as independent variables in multivariate analyses.
Besides, there are some issues that need to be addressed/clarified to ensure that the data fully
support the statements and conclusions made.
I suggest that the Authors give some comments on the following points:
1. In the summary and the text, change “may be an effective predictor of NAFLD risk” with
“may be associated to NAFLD”, since this is not a prospective study.
2. The Authors say (line 57) that “under fasting conditions, RC is cholesterol-containing very-
low-density lipoprotein, intermediate-density lipoprotein and chylomicron remnants”. This is
not correct. Under fasting condition, RLP-C is the cholesterol contained in very-low-density
lipoproteins, which originate in the liver, and in their relatively TG-depleted remnants (IDL),
while chylomicron remnants are present only in non-fasting condition.
3. In addition to the references reported in line 63, a further study demonstrated that NAFLD
was independently associated with higher circulating RLP-C, and that high RLP-C levels were
predictive of major cardiovascular and cerebrovascular events in patients with NAFLD (J. Clin.
Med. 2018, 7, 378; doi:10.3390/jcm7110378).
Review for 10.1186/s12876-022-02216-x (2022)

Title: Remnant cholesterol/high-density lipoprotein cholesterol ratio is a new powerful tool for
identifying non-alcoholic fatty liver disease
Version: 2 Date: 24 Feb 2022
Reviewer's report:
This observational study aimed to explore the correlations between RC/HDL-C ratio NAFLD
risk. The main advantage of this study is a rather large sample size. Different multivariate models
were tested and RoC analysis was done. The study claims the RC/HDL-C index is a  potentially
useful marker for NAFLD risk. However, this statement should be taken with caution taking
into account the limitations acknowledged (absence of hepatic biopsy to confirm the diagnosis,
gender inequality, insulin resistance assessment, etc) by the authors.
It should be clarified to the readers that ROC analysis indicates the ability of the RC/HDL-C
index to discriminate healthy individuals from NAFLD patients, thus indicating the NAFLD
presence rather than the risk for developing NAFLD.  This statement should be corrected
throughout the manuscript, as risk assessment should be done by a different study protocol.
A prospective study on healthy individuals should be done to validate this claim and further
elucidate other findings of this study.
Review for 10.1186/s12876-022-02212-1 (2022)

Title: Deep Learning Model Can Improve the Diagnosis Rate of Endoscopic Chronic Atrophic
Gastritis: A Prospective Cohort Study
Version: 2 Date: 15 Jan 2022
Reviewer's report:
I read with interest the study by  Quchuan Zhao and  Tianyu Chi entitled "Deep Learning Model
Can Improve the Diagnosis Rate of Endoscopic Chronic Atrophic Gastritis: A Prospective
Cohort Study". I think that the study is well written with a solid background, exhaustively
described methods,  robust statistical methods and well-presented results with efficient tables
and figures.
What emerges from this paper is that this tool may  improve the diagnostic performance of
endoscopists and this will  ultimately be of benefit for patients.
Ihave only  a few comments:
One is  on the "Deep learning model training and testing" described in the Methods section. I
wonder whether these data on the U-NET network used to build the real-time video monitoring
diagnostic model for endoscopic CAG based on DL used in this study was previously published
as no reference is stated.
I would also suggest to include in the Discussion section that endoscopical diagnosis of CAG
is  a skill much more diffuse in Asian countries, as in Western countries diagnosi of CAG still
relies  mainly on pathology.
In  the Methods section I did not read the type of endoscopes used,  did the authors use
magnification, high-resolution or chromoendoscopy techniques as BLI or NBI.
Review for 10.1186/s12876-022-02212-1 (2022)

Title: Deep Learning Model Can Improve the Diagnosis Rate of Endoscopic Chronic Atrophic
Gastritis: A Prospective Cohort Study
Version: 2 Date: 26 Jan 2022
Reviewer's report:
Quchuan Zhao's manuscript aims to demonstrate the contribution of deep learning to the
recognition of gastric glandular atrophy lesions.
The model was trained on a database of 5290 images from 1711 patients.  In this database, 4175
images concerned glandular atrophy of different grades of severity. The manuscript was evasive
on the histopathological evaluation of glandular atrophy, although this is the only determinant
factor independent of the observer. It would have been mandatory to train the model from
photographed sites where oriented biopsies would performed. Only the analysis of which would
have determined the nature of the lesions to train the deep learning network.
Without this feature, the reader has the impression that the deep learning network was trained
to recognise the lesions identified by the endoscopists of the centre.
This negative impression is even more pronounced as the diagnostic performance of deep
learning has not been compared with that of endoscopists from other centres.
Review for 10.1186/s12876-022-02198-w (2022)

Title: Effect of alcohol on clinical complications of hepatitis virus-induced liver cirrhosis: a
consecutive ten-year study
Version: 1 Date: 12 Dec 2021
Reviewer:  Antonio Mirijello
Reviewer's report:
The manuscript is interesting and addresses an hot topic in the field of hepatology: the
relationship and the effect of alcohol on the natural history of viral cirrhosis.
However, I have som concerns (MAJOR) that should be solved by Authors:
- Alcoholic liver disease (ALD):  this definition is extensively used throughout the text (abstract
and main body). However,  I would suggest to replace "alcoholic liver disease" with "alcohol-
induced liver disease" or "alcohol-associated liver disease".
- Alcohol abuse: this definition is extensively used throughout the text (abstract and main
body).  However, the DSM-5 has abandoned the dichotomy between alcohol abuse and alcohol
dependence and replaced them with the broader  definition of AUD (alcohol use diserder).  I
would suggest to Authors to replace "alcohol abuse" in the abstract and in the text with AUD or
excessive alcohol consumption  or heavy alcohol use, as appropriate.
-  INTRODUCTION, liner 13-16, the explanation od markers of alcohol abuse  lacks of
a reference. Please cite "Addolorato G, Vassallo GA, Mirijello A, Gasbarrini A. Diagnosis
and Management of Alcohol Use Disorder in Patients with Liver Disease: Lights and
Shadows. Neurotherapeutics. 2020 Jan;17(1):127-141. doi: 10.1007/s13311-019-00802-8.
PMID: 31713188; PMCID: PMC7007485".
- MATHERIAL AND METHODS:  speaking of  alcohol consumption and alcohol abstinence.
How did you record alcohol consumption and/or alcohol abstinence? Basing on patients report?
Basing on the report of a relative? By using TLFB?
- DISCUSSION, LIMITATIONS SECTION: The main limitation of this study is represented
by the retrospective design.  Authors should quote that the retrospective design of the study
represents by itself a limitation, give the lack of an a priori evaluating protocol.
In addition, Authors should also quote that the effect of alcohol abstinence on viral replication
and /or on the  antiviral treatment efficacy could not be explored by this  study design.
MINOR COMMENTS:
- INTRODUCTION, first line:  Would you like to mention the etiologies in order of prevalence?
Or alphabetically?
- MATHERIAL AND METHODS, first line: instead of saying "our Horpital", could you define
it: e.g. name, city, tertiary care, nr of beds, teaching, etc.
- DISCUSSION: What about other biomerkers of alcohol intake/alcohol abstinence, e.g.
Carbohydrate Deficient Transferrin (CDT)?
Review for 10.1186/s12876-022-02198-w (2022)

Title: Effect of alcohol on clinical complications of hepatitis virus-induced liver cirrhosis: a
consecutive ten-year study
Version: 3 Date: 01 Mar 2022
Reviewer:  Antonio Mirijello
Reviewer's report:
Authors satisfactorily address all  the raised comments.
Please revise reference 4 (it lacks of Journal name).
Review for 10.1186/s12876-022-02200-5 (2022)

Title: Construction of immune-related lncRNA signature to predict aggressiveness, immune
landscape, and drug resistance of colon cancer
Version: 2 Date: 23 Oct 2021
Reviewer's report:
In the manuscript#the authors took advantage of the transcriptome data of the TCGA-COAD
cohort to construct two immune-related lncRNA-based models which predict the clinical
outcomes of colorectal cancer patients. Then the authors further compared the immune cell
infiltration, the expression of TGFB1 and LAG3, predicted drug susceptibility between high-
risk and low-risk groups. Functional GSEA analyses were also performed. The overall design
of this study is sound. However, there are questions/comments for the authors as follows:
1)The language in the manuscript should be further polished by a native English speaker.
2)The LASSO regression model. The description of this model is not sufficiently detailed. Why
was this model chosen? As far as I know, the result of each run for the model is quite different.
So what are the criteria for final model determination?#AIC, BIC or other criteria). These have
to be explained in detail.
3)The authors developed two risk models in this study: the pair-risk model and the exp-risk
model. No comparison of these two models was conducted. The GSEA analysis was only
performed based on the exp-risk model. Therefore, readers may get confused about the purpose
and the point of establishing two models.
4)No FDR or multiple hypothesis testing was done. In other words, P values were not adjusted,
such as Fig.2A-2B#Fig 3C#Fig. 4E-G, et al.
5)As the author only utilized that the data of the TCGA-COAD cohort instead of the combination
of TCGA-COAD and TCGA-READ, the 'colorectal cancer' is not an accurate description. There
seems to be no R package called 'survivor.' The primary endpoint of this study#DFS or OS) was
missing in the manuscript.
6)Suggestions for figures and supplementary materials. To make the results more readable, it is
recommended that Figure 2A-B only displays the result for 11 core immune lncRNAs. Results of
the rest meaningful irlncRNAs can be added to the supplementary materials. Besides, the authors
calculated the infiltration of the immune cells with seven acknowledged algorithms, which
deserves recognition. However, overlapped and consistent results should be emphasized, as this
could give us more confidence in the authors' conclusions. Meanwhile, consider integrating
the consistent results into one single graph for readability instead of multiple boxplots. Please
consider other types of plots for presentation.
7)Apart from LAG3, multiple classical immune checkpoints should be included in the analysis,
such as PD-1/PD-L1, CTLA4, TIM3#TIGIT, et al. In figure 7C-G#the IC50 of several drugs
were compared between two risk groups. A detailed description of these drugs should be
included in the main text.
8)The risk models proposed by the authors were not validated in an independent cohort.
9)The discussion section should emphasize the role of selected 11 lncRNAs in cancers and their
immune correlation in cancers.
Review for 10.1186/s12876-022-02200-5 (2022)

Title: Construction of immune-related lncRNA signature to predict aggressiveness, immune
landscape, and drug resistance of colon cancer
Version: 2 Date: 05 Nov 2021
Reviewer's report:
The overall design idea of the article is clear and the model design is reasonable. It is suggested
to answer several questions and make necessary modifications.
Major issues:
1. As mentioned in the manuscript, the authors established a pairs-risk model and an exp-risk
model respectively and then combined them to predict the prognosis. What are the advantages
of these three models, that is, under what circumstances to choose a model?
2. The author uses the data in the TCGA database to establish the model. To ensure the stability
and credibility of the model, should other datasets be used for verification? (such as datasets
in GEO).
Minor issues:
1. In the discussion, the authors should emphasize their model's strengths over other prognostics
scoring systems.
2. The authors found two immune-correlative genes, TGFB2 and LAG3. However, there is no
relevant discussion on these two genes.
3. It is suggested that it may be better to rearrange the picture. For example, in Figure 6B-X,
the positive and negative immune cells correlation with the risk value of the model, are listed
together to facilitate readers' understanding. In addition, the same is true in Figure 7. It would
be better to list 2 genes and 5 chemotherapeutic drugs respectively.
4. Needs some language corrections before being published. For example, spelling mistakes in
the name of the corresponding author on the title page, “Baoqing Jia” for “Boqing Jia”. Other
small grammatical errors need to be corrected.
Review for 10.1186/s12876-022-02200-5 (2022)

Title: Construction of immune-related lncRNA signature to predict aggressiveness, immune
landscape, and drug resistance of colon cancer
Version: 5 Date: 09 Dec 2021
Reviewer's report:
After the manuscript is revised, the content is expressed more accurately. However, there are
still problems in the writing and wording of the article. It is recommended to invite professional
institutions to conduct language editing before publication.
Review for 10.1186/s12876-022-02200-5 (2022)

Title: Construction of immune-related lncRNA signature to predict aggressiveness, immune
landscape, and drug resistance of colon cancer
Version: 5 Date: 19 Jan 2022
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: This manuscript deals with a bioinformatic analysis of immune
related long non coding RNA (irlncRNA) in colorectal carcinoma (CRC) associated to biological
features of CRC and host immune response to predict aggressivity, resistance to therapy and
immune infiltration. This analysis is well performed and of interest.
REQUESTED REVISIONS:
No experimental data are shown, and an experimental validation of the conclusions has been
performed.
This is the main limitation of this study. The different lncRNA identified as relevant in the
“construction” of the signature are not related to actual experimental data validated in CRC cell
lines or in CRC organoids to reinforce and demonstrate the validity of the findings reported.
This limitation is mentioned in the text at the end of this manuscript.
No clear explanation of the reason why, among the plethora of potential markers, the authors
have selected LAG3 and TGFbeta as markers for the correlation analysis of immune genes.
Furthermore, it has not been demonstrated that the analysis of other markers is not effective. It is
well known that several inhibitory receptors are present in the microenvironment. It seems that
looking at LAG3 and TGF, one can categorize all CRC. Is there any relation with the irlncRNA
with the expression and function of LAG-3? What about the association with the expression and
function of CTLA4, PD1, KIR, LIR, LIR, TIGIT, CD300, LAIR (without taking into account
the others) on specific immune cells within the microenvironment.
The methodology appears well organized, and the topic is of interest. However, the data remain
a very nice analysis and suggestion without an evident applicability into the clinic as well as to
get further insight on the biology and immune response in CRC.
Review for 10.1186/s12876-022-02200-5 (2022)

Title: Construction of immune-related lncRNA signature to predict aggressiveness, immune
landscape, and drug resistance of colon cancer
Version: 7 Date: 18 Feb 2022
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: The authors have replied to my concerns adequately, and they have
inserted some of these replies in the text and in a supplemental figure. The manuscript has been
improved.
ADDITIONAL REQUESTS/SUGGESTIONS:
No, I do not have any concern with this manuscript"
Review for 10.1186/s12876-022-02197-x (2022)

Title: Additive effect of evaluating microsurface and microvascular patterns using magnifying
endoscopy with narrow-band imaging in gastric cancer: a post hoc analysis of a single- center
observational study
Version: 1 Date: 05 Jan 2022
Reviewer's report:
There are many reports on the diagnostic performance of MS and MV in the diagnosis of gastric
cancer using ME-NBI. In order to increase the scientific strength of this paper, the following
modifications should be made.
Comment 1: The non-cancerous image used in this study appears to be the gastric mucosa
around the lesion obtained prior to ESD. It is necessary to describe whether the non-cancerous
image is erosion due to inflammation, the surrounding intestinal metaplasia mucosa, or the
mucosa without atrophy. The characteristics of the histopathology of the non-cancerous image
are important information and should be additionally described.
Comment 2: Please clearly describe in each MS and MV what findings are observed in this
analysis to diagnose cancer.
Comment 3: Table 3 is confusing and should be changed to something that is easier for the
reader to understand.
Comment 4: Table 5 seems to show the characteristics of lesions that are difficult to diagnose
by MV. Since the notation of the table is complicated, it should be revised to a table that is easy
for the reader to understand.
Review for 10.1186/s12876-022-02197-x (2022)

Title: Additive effect of evaluating microsurface and microvascular patterns using magnifying
endoscopy with narrow-band imaging in gastric cancer: a post hoc analysis of a single- center
observational study
Version: 1 Date: 28 Jan 2022
Reviewer's report:
Congratulations for collecting nice data on the important topic. I have some concerns regarding
the manuscript which are as follows:
Major
1. I cannot see the information about control group (true negatives – non-cancerous lesions/non-
cancerous parts of the resected cancerous lesions confirmed in the histopathological assessment)
how was it selected? It is crucial for the analysis performed in the study. If only photographs
of parts of the lesions were assessed, was it confronted with histopathology (actual spot that
was photographed)? If so it should be stated in methods section. If not the results are actually
agreement with the experts who selected and confirmed photographs of parts of the lesions being
neoplastic and non-neoplastic not actual analysis of cancerous and non-cancerous lesions/tissue.
2. In the Evaluation criteria of methods section authors are explaining how the agreement was
assessed however it should be corrected. That data has to be showed and compared for example
as Kappa value (not as percentage) such as in other research.
Taveira F et al. The Colon Endoscopic Bubble Scale (CEBuS): a two-phase evaluation study.
Endoscopy. 2022 Jan;54(1):45-51. doi: 10.1055/a-1331-4325. Methods, result and discussion
should be modified accordingly.
3. Table 4. If analysis is not comparing only MS and MV data regarding MS+MV vs MS alone
should be also provided.
Minor
1. In the Methods section no data regarding histopathological classification is provided (for
example diagnosis of cancer according to Vienna classification).
2. Methods section sentence “The VS classification system was used for diagnosis” of lesions?
3. Methods section: there is no need to explain what accuracy (ACC) is. The authors should
explain all values (NPV, PPV, sensitivity, specificity) or none of them.
4. Methods section sentence “H. pylori-uninfected cases were defined as follows:…” the patient
should met one or all of the criteria? – it should be clarified. Also, patients who did not meet
the “H. pylori-infected with eradication group” criteria were infected without eradication? It
should be stated.
5. Results – part” after adding the history of H. pylori infection to the background characteristics
of the patients included in the previous study [12].” Is unnecessary.
6. Discussion section: Two sentence ale doubled “While some previous reports have indicated
that gastric cancer can be diagnosed based on MV alone [9, 10],” and “some studies have
reported that assessments based on MV alone are feasible for diagnosis [9–11].” Also, it should
be clarified if reference 11 is suitable or not.
7. Table – please clarify the “gastric tube” term.
Review for 10.1186/s12876-022-02197-x (2022)

Title: Additive effect of evaluating microsurface and microvascular patterns using magnifying
endoscopy with narrow-band imaging in gastric cancer: a post hoc analysis of a single- center
observational study
Version: 2 Date: 14 Feb 2022
Reviewer's report:
According to the reviewer's comments, the manuscript has been properly revised. With this
revision, this paper has been updated in an easy-to-understand manner for readers.