JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-01956-6 (2021)

Title: Comparison of the efficacy and safety between palliative biliary stent placement and duct
clearance among elderly patients with choledocholithiasis: A propensity score-matched analysis
Version: 1 Date: 05 Sep 2021
Reviewer's report:
The current study was a single center retrospective study to compare long-term outcomes after
endoscopic biliary stent placement and complete stone removal for elderly patients with common
bile duct stones. I suppose that this study contains an important information, but I have several
comments as follows.
1. The current study is single center retrospective study. Please clarify this point in the method
section.
2. The patients with surgically altered anatomy (SAA) were included in this study. Did all
patients with SAA undergo ERCP using balloon endoscope?
3. The sentence that “The EBS group had a significantly higher proportion of elderly individuals”
seems odd, because the inclusion criteria of this study is elderly patients as authors described
in the methods section.
4. Fourteen covariates were selected to calculate propensity score, but these variables were not
clarified in the main document.
5. Please show the rate of patient who underwent planned cholecystectomy after ERCP. The rate
of cholangitis in patients after complete stone removal seems to be low compared with previous
studies. I wonder you could not accumulate actual number of patients who developed cholangitis
after complete stone removal.
6. One cholecystitis was reported as late adverse event in Table 2. No patients after complete
stone removal did not develop cholecystitis after the long follow-up period?
7. Follow-up strategy after ERCP should be described. Were routine follow-up imaging studies
or blood test examined in outpatient basis with regular interval?
8. As you described in the discussion section, some patients were difficult to follow their long-
term outcomes. At least patients of their follow-up period within 30-days should be excluded
from the analyses.
9. Were patients with recurrent bile duct stone after complete stone removal were repeatedly
included in this study?
10. In the Table 1, the rate of patients of their performance score 3 is documented. Did you
exclude patients with their performance score 4? I assume that consecutive patients were
included in this study. EBS without stone removal was particularly important in patients PS 4.
11. The median duration of cholangitis-free periods in patients with palliative EBS was 596
days in this study. Usually, patients after plastic stent placement were recommend biliary stent
exchange in 3-6 months interval. Please describe the authors opinion about this long cholangitis-
free period after EBS.
12. The rate of patients who used dual or triplet antithromtobic agents should be documented.
13. The preferable long-term outcome after complete stone removal compared with EBS is
already known, and guidelines recommended stone removal. The authors intended to show
natural history of EBS without stone removal, but due to the small sample size, the study result
seemed to contain a lot of bias.
Review for 10.1186/s12876-021-01956-6 (2021)

Title: Comparison of the efficacy and safety between palliative biliary stent placement and duct
clearance among elderly patients with choledocholithiasis: A propensity score-matched analysis
Version: 2 Date: 29 Sep 2021
Reviewer's report:
The authors appropriately revised the manuscript in accordance with the comments.
Review for 10.1186/s12876-021-01956-6 (2021)

Title: Comparison of the efficacy and safety between palliative biliary stent placement and duct
clearance among elderly patients with choledocholithiasis: A propensity score-matched analysis
Version: 2 Date: 02 Oct 2021
Reviewer's report:
I have no further comments. The article is acceptable.
Review for 10.1186/s12876-021-01945-9 (2021)

Title: Role of endoscopic ultrasonography for differential diagnosis of upper gastrointestinal
submucosal lesions
Version: 0 Date: 05 Jul 2021
Reviewer's report:
The authors presented their experience with diagnostic B mode EUS in the differential diagnosis
of SMLs.
1) The title should be changed to "...differential diagnosis..."
2) Introduction, line 59. It is incorrect to state that identification of SMLs with endoscopy is
difficult. You may want to state "Differential diagnosis of...is difficult"
3) Line 65: I do not understand the term "hierarchal" here. Maybe you want to say "wall layer
structure"?
4) Methods, line 90: please replace "microprobe" with "miniprobe"
5) Line 93: water infusion does not sound correct. I would write "lumen filling with water"
6) Results, line 125: please replace "pathologies"  with "histological types"
7) Line 155, please amend as follows: "Sensitivity, specificity and predictive value of the
originating layer on EUS to determine the pathological nature of the submucosal lesions"
8) Discussion: please add a paragraph to discuss the limitations of the current study.
In particular, I would quote:
a) retrospective design;
b) the lack of CH-EUS (please add some reference in this regard, e.g. Kamata K, Takenaka
M, Kitano M, et al. Contrast-enhanced harmonic endoscopic ultrasonography for differential
diagnosis of submucosal tumors of the upper gastrointestinal tract. Journal of Gastroenterology
and Hepatology (Australia) 2017;32:1686-1692.);
c) the lack of EUS-FNA/B (you can cite: Jenssen, C., Hocke, M., Fusaroli, P., et al. EFSUMB
Guidelines on Interventional Ultrasound (INVUS), Part IV - EUS-guided interventions:
General Aspects and EUS-guided Sampling (Short Version). Ultraschall in der Medizin
2016;37:157-169.)
9) Please go through your text from A to Z to revise several language issues that require polishing
Review for 10.1186/s12876-021-01945-9 (2021)

Title: Role of endoscopic ultrasonography for differential diagnosis of upper gastrointestinal
submucosal lesions
Version: 0 Date: 10 Jul 2021
Reviewer's report:
The article is a well written retrospective study on EUS based SMLs assessment. However this
just does not add anything to current knowledge.
According to author report, the only news
would be this:  "Additionally, the maximum diameters of the lesions were compared and the
results suggested that the mean maximum diameter of stromal tumors was significantly greater
than that of leiomyomas. This may provide a certain reference for differentiation between the
two types of SMLs "
Comparing the size of leiomiomas and GIST as a discriminating feature is misleading
considering the first are mostly esophageal and the second were mainly gastric. Esophageal
lesions are likely to cause early symptoms compared to gastric lesions being investigated and
diagnosed earlier. It is a matter of location more than size.
A part from the clearly misleading statment on lesion size in suggesting one etiology more than
the other, all other conclusions are already well known. I would at least expect info on contrast,
elastography, needles... maybe that could have been more interesting.
Review for 10.1186/s12876-021-01937-9 (2021)

Title: Survival analysis of stage II gastric cancer patients after D2 gastrectomy: A Chinese
people-based research
Version: 2 Date: 13 Feb 2021
Reviewer:  Tsutomu Hayashi
Reviewer's report:
It is retrospective observational study investigating factors influencing survival focusing on
pStageII gastric cancer patients. This article gives us the important information concerning the
problem which we are facing. The methodology and interpretation of the results is appropriate.
The results are so interesting and informative that the paper is worth published. However, several
points need to be addressed.
1) Recently, the duration of postoperative adjuvant chemotherapy has proven to have a
significant effect on survival in phase III trial; Lancet Gastroenterol Hepatol 2019; 4: 208–16.
This phase III trial aimed to shorten the duration of adjuvant chemotherapy for the patients with
pStageII gastric cancer. This paper should be cited and discussed.
2) Regimen of the adjuvant chemotherapy should be clarified. I f this is not possible, it should
be stated that the regimen has a minor impact on the results in limitation section.
Review for 10.1186/s12876-021-01937-9 (2021)

Title: Survival analysis of stage II gastric cancer patients after D2 gastrectomy: A Chinese
people-based research
Version: 2 Date: 07 May 2021
Reviewer's report:
The authors aimed to confirm the role of adjuvant chemotherapy in the treatment of stage
II gastric cancer and determine some prognostic factors for the establishment of a prediction
model to guide individualized treatment for stage II gastric cancer. They concluded that adjuvant
chemotherapy can improve OS in stage II gastric cancer patients. In addition, Tumor size,
CEA, and N stage are prognostic factors, and age, tumor location, and T stage are independent
prognostic factors, thus providing significant evidence for doctors to identify patients with poor
prognosis and helping guide individual therapy. In the first place, the ACTS-GC study and the
CLASSIC study both concluded that adjuvant chemotherapy for patients with Stage II/III gastric
cancer was confirmed to improve prognosis. The subgroup analyses in both studies revealed that
prognosis of patients with Stage II gastric cancer significantly improved in the final analyses.
Therefore, the first aim and the first conclusion are nonsense. Moreover, to achieve the second
purpose, the authors should propose some examples of which patient should receive adjuvant
chemotherapy and which patient should not.
Stage II in TNM 8 is not identical to that used in the ACTS-GC and the CLASSC studies. The
most important difference is that the tumors with subserosa invasion is classified to T3 in the
TNM8 while those were classified to T2. This difference should be addressed and considered
in the manuscript.
Review for 10.1186/s12876-021-01937-9 (2021)

Title: Survival analysis of stage II gastric cancer patients after D2 gastrectomy: A Chinese
people-based research
Version: 4 Date: 31 Jul 2021
Reviewer's report:
Age#60, linitis plastica or T4 were risk factors for prognosis independent from the administration
of adjuvant chemotherapy. This means that patients with Age#60, linitis plastica or T4 have poor
prognosis even if they receive adjuvant chemotherapy. Therefore, the conclusion that patients
with these risk factors should receive adjuvant chemotherapy for prolonging overall survival
time is not justifiable.
In the Discussion section (p11, Line 7-9), “T” needs to be corrected to “N”.
T1N3b in the 8th edition AJCC which is classified to stage IIIB is classified to T1N3 and Stage
4 in the 6th edition AJCC. In other words, T1N3b in the 8th edition is not originally included in
stage II in the 6th edition AJCC, so please delete T1N3b in Page 11, Line 9.
Review for 10.1186/s12876-021-01943-x (2021)

Title: The clinical significance of preoperative serum fibrinogen levels and platelet counts in
patients with Gallbladder carcinoma
Version: 1 Date: 01 Sep 2021
Reviewer's report:
Well written study.
I recommend to report in the discussion other potential molecular prognostic factors of
carcinogenesis, as reported in other neoplasms (cite the following:
- PMID: 23845075
- PMID: 29220698
- PMID: 25915713
Review for 10.1186/s12876-021-01943-x (2021)

Title: The clinical significance of preoperative serum fibrinogen levels and platelet counts in
patients with Gallbladder carcinoma
Version: 1 Date: 01 Sep 2021
Reviewer's report:
My main concern is on the correlation analysis for prognosis. Authors should conduct a Cox
regression analysis and report hazard ratio (along with 95% CIs in a specific table).
Univariate analysis should be conducted for main baseline variables, then significant factors in
univariate analysis should be entered to a multivariate model.
Review for 10.1186/s12876-021-01922-2 (2021)

Title: C-reactive protein is associated with postoperative outcomes in patients with intestinal
Behçet’s disease
Version: 1 Date: 13 Apr 2021
Reviewer's report:
Major points
1. Some intestinal BD cases that did not meet the ISG criteria were included as "suspected cases",
but analysis with only cases that met the criteria should also be included in the analysis.
2.  Authors stated "Surgeries not associated with intestinal lesions were excluded", but a
flowchart should be provided to show how many cases were screened and how many cases were
included in the analysis.
3. the definition of "CRP within 5 days after surgery" is ambiguous. There is a wide range from
1 to 5 days postoperatively, and the numerical value of CRP fluctuates greatly, so the number
of days should be strictly determined and evaluated.
4. The overall disease activity of Behcet's disease at the time of surgery may be more important
than CRP alone, and should evaluate the relationship between overall activity such as BDCAF
and rate of relapse.
5. Recently, the use of TNF antibodies has reduced the number of surgical cases in intestinal
Behcet's disease, but is there a change over time? Has there been a change over time? Is there
a possibility of preventing relapse by using TNF?
Minor points
1. Some references are missing (page 4 line 83, page 10, line 209, etc.)
2. The title of the paper needs to be changed, as it is not possible to determine predictors based
on retrospective studies. Rather, the term "associate" would be better.
3. Table 1 should also include other types of Behcet's disease phenotypes such as skin
manifestations, oral ulcers, genital ulcers, eye, HLA-B*51, etc.  "immunomodulator" should
include specific agents used for the treatments.
Review for 10.1186/s12876-021-01922-2 (2021)

Title: C-reactive protein is associated with postoperative outcomes in patients with intestinal
Behçet’s disease
Version: 1 Date: 15 Apr 2021
Reviewer's report:
Thank you for reviewing the manuscript titled “ Role of C-reactive protein in predicting
postoperative outcomes in patients with intestinal Behçet’s disease”
The present manuscript is well written regarding the importance of measuring serum CRP
level immediately after surgery to predict postoperative complication and clinical recurrences.
Because intestinal Behçet’s disease is relatively rare disease, therefore there few evidences about
usefulness of biomarkers including CRP in patients with intestinal Behçet’s disease. I have
several comments described as below.
1 The authors assessed CRP levels within 5 days after surgery. This reviewer is considering that
CRP levels are quite different among Day1, Day3 and Day5. The authors should discuss about
the differences of CRP levels depending on the days after surgery.
2 Also, CRP levels, albumin levels, the presence of large ulcer (volcano ulcer), fistula, or abscess
prior to surgery should be collected and then, relationship between postoperative complication
and disease severity/serum markers should be assessed.
3 As Table 4 and Figure 1 indicate, the diagnostic value does not seem to be so well. The authors
should discuss the benefit (easy?, non-invasive?, low cost?) and limitation of measuring CRP
just after surgery to assess the complication and prognosis.
Minor
1 For assessment of prognosis, median (mean) follow-up period should be presented.
2 Number of events including clinical relapse, re-operation, and re-admission should be
presented.
3 It should be clarified whether the presence of ulcer with volcano type before surgery was not
associated with postoperative surgy, described as above.
4 Please cite the reference regarding higher complication rate in BD than Crohn’s disease (page
4 L 78).
Review for 10.1186/s12876-021-01938-8 (2021)

Title: Impact of Diagnostic Delay to the Clinical Presentation and Associated Factors in
Pediatric Inflammatory Bowel Disease: A Retrospective Study
Version: 2 Date: 01 Jun 2021
Reviewer's report:
E Sulkanen and colleagues present factors associated with time to referral prior to diagnosis of
inflammatory bowel disease.  They identify abdominal pain as a factor associated with delayed
diagnosis, hematochezia as a symptom associated with a shorter delay, and ulcerative colitis
with less delay compared to Crohn's disease.   While these could be significant findings, I have
several concerns I would recommend that the author's address
Major Concerns:
1. As they mention in their discussion, time to referral may change over time.  Therefore, the
authors should indicate in their methods over what time frame these patients presented for
referral.
2. We know fecal calprotectin's sensitivity/specificity/positive predictive value is dependent
upon what quantitate cutoff is used.  The author's should provide reference for their value of
<100 microgram/g (which seems lower than what most other literature would suggest is used).
3. As their median delay was 5 months, would recommend additional groups for delay rather
than >6 or <6 by separating less than 6 into less than 3 and 3-6 months
4. Since the authors found the majority of delay is prior to referral, would recommend the author's
use a non-IBD diagnosis as a control group.  In addition, do the authors have data on time of
symptoms onset to presentation to their primary care provider?
4. Table 1 and Table 2 are missing any statistical analysis.  While their abstract provides a p-
value for CD vs UC, this is not apparent in their text nor table/figures
5. Table 3 is missing diagnosis as a variable.  Since symptoms may vary among diagnosis, would
recommend multiple regression to determine if symptoms or diagnosis is driving the difference.
6. Would recommend looking at initial disease activity score (PUCAI and either PCDAI or the
short PCDAI) to determine if this varied based upon time to diagnosis.  Related, authors could
determine if disease location was a factor associated with diagnostic delay.
7. The manuscript's title refers to the impact of diagnostic delay.  To answer this question,
the author's should provide some follow-up data to determine the impact on disease control
particularly since table 4 fails to identify any complication/co-morbidity present at the time of
diagnosis.
Minor concerns:
1. The first sentence in the abstract is a bit awkward and more declarative than would be
recommended (this should be the point the manuscript is trying to conclude?)
2. The  first sentence within the introduction is very broad knowledge and is well known so does
not need to be included.
3. Figure 1 does not seem to add much to the manuscript and likely could be removed.  If there
was difference in time to diagnosis associated with disease location, then this could become
more relevant.
Review for 10.1186/s12876-021-01938-8 (2021)

Title: Impact of Diagnostic Delay to the Clinical Presentation and Associated Factors in
Pediatric Inflammatory Bowel Disease: A Retrospective Study
Version: 3 Date: 26 Aug 2021
Reviewer's report:
I have no further comments. The authors have addressed my points very well. Even query 18
was solved by the deep revision of the manuscript. I think that the methodology is clearer now,
making findings relevant accordingly. My congratulations!
Review for 10.1186/s12876-021-01938-8 (2021)

Title: Impact of Diagnostic Delay to the Clinical Presentation and Associated Factors in
Pediatric Inflammatory Bowel Disease: A Retrospective Study
Version: 3 Date: 18 Sep 2021
Reviewer's report:
The authors have responded appropriately to my initial feedback, although sample size and
retrospective design limited their ability for full revision
Review for 10.1186/s12876-021-01934-y (2021)

Title: Sodium nitroprusside protects HFD induced gut dysfunction via activating AMPK#/
SIRT1 signaling
Version: 2 Date: 22 Dec 2020
Reviewer's report:
In this study, the authors have investigated the potential mitigating effects of the NO donor,
sodium nitroprusside (SNP). Using the Caco-2 cells, they show that LPS reduces the expression
of tight junction proteins, which is reversed by SNP treatment. Using the high-fat diet-fed mouse
model, they show that SNP reverses some of HFD feeding effects. The results appear to be
interesting, and the study is mechanistic. However, there are numerous issues in the study design
and presentation, including a lack of crucial control groups.
Major
1. Fig 1: Perform densitometric analysis and present data in graphs with statistical analysis. Are
there effects of LPS and SNP associated with similar changes in the epithelial permeability?
2. Fig. 1C&D: This study needs to include NC-siRNA and siAMPK controls.
3. Fig 2: The study needs an SNP control group.
4. Fig. 2: The data show that the bodyweight increased by HFD in almost entirely reversed
by SNP. However, the fat mass increase is reversed only partially. The data presented is the
total fat mass, which means the fat per g body weight is even higher. This discrepancy begs the
question of what is the cause of reduced body weight? The caption of this figure in the legend
is, therefore, misleading.
5. Fig 3H: the magnification of the HFD group is taken from the half of the section that seems
to be affected while the other half of the section appears normal. Is this consistent with sections
from other animals, or is it a sectioning artifact?
6. The HFD+SNP intestine appears to have many goblet cells. An explanation of this observation
requires it is to include an SNP control group.
Minor
1. Figure legend: please describe the experimental setup rather than summarizing the results.
2. There are too many typos and grammatical errors. The manuscript needs to be professionally
checked for English.
Review for 10.1186/s12876-021-01934-y (2021)

Title: Sodium nitroprusside protects HFD induced gut dysfunction via activating AMPK#/
SIRT1 signaling
Version: 2 Date: 19 Jan 2021
Reviewer's report:
1. The methods used in this manuscript should note the reference.
2. How many animals for experiment? What's the house condition?
3. The language of this manuscript need to be improved.
4. why the expression of ZO-1 protein with the treatment of SNP is much higher than blank
control?
5. Only body weight changed, fat mass and fasting blood glucose content were measure, which
is not enough for evaluation obesity.
6.  The gut microbiota analysis was not enough,such as the richness (ACE and Chao1 indexes)
and diversity (Shannon and Simpson indexes) of microbial communities.
7. The relationship between the AMPK pathway and the intestinal barrier was not shown in the
manuscript.
8.The influence of NO on the AMPK pathway and tight junction proteins should be discussed
fully.
9. Each aspect of the study is relatively simple and needs to be further studied.
Review for 10.1186/s12876-021-01934-y (2021)

Title: Sodium nitroprusside protects HFD induced gut dysfunction via activating AMPK#/
SIRT1 signaling
Version: 5 Date: 16 Apr 2021
Reviewer's report:
This is a revised manuscript. Previous review raised many concerns and the authors have made
great effort to answer most of the questions and has improved the manuscript. My one concern
remains is the lack of SNP control in Fig. 2. It is important to know if SNP reduces the basal
mesenteric fat mass and blood glucose, and the partial reduction in HFD group is that effect.
Review for 10.1186/s12876-021-01934-y (2021)

Title: Sodium nitroprusside protects HFD induced gut dysfunction via activating AMPK#/
SIRT1 signaling
Version: 5 Date: 07 May 2021
Reviewer's report:
The manuscript has been revised as suggested previously, but it still needs revision prior to
publication. Besides, the language need to be further improved, there are still many typos and
grammatical errors, it is unacceptable at its current form, please seek for help from native English
speakers or professionals.
Line 31 mechnism---mechanism
Line 30 Please delete the extra space between “to” and “activate”, similar modifications should
be done throughout the text (i.e. line 54, 61 and 77).
Line 42 Please add space between “complicated” and “by”, same mistakes can be found at line
51, 85 and 230 etc. Please check again throughout the manuscript.
Line 44, implied-imply, alleviate-alleviates
Line 101 Please insert space between the numeral and the unit, i.e. 1mg/mL should be changed
to 1 mg/mL.  The only two exceptions are % and #.  Similar modifications should be done
throughout the text, including all figures.
Line 120 “mg/ml” should be changed to “mg/mL”, please keep consistent with the former.
Similar modifications should be done throughout the text (i.e. line 135-136, ng/mL instead of
ng/ml).
Line 131 The procedure for cell culture is too simple, lacking some key information, such as
the density of cells, types of plates, cell passage number and cell culture condition, etc. Please
add the above and other necessary information.
Line 196, 207, 236, please replace “compared to” by “compared with”, as the phrase compare
to is used when the intent is to assert, without the need for elaboration, that two or more items
are similar. Whereas the phrase compare with is used to juxtapose two or more items to illustrate
similarities and/or differences.
Line 257 Please replace the word “involed” by “involved” and add “be” before it.
Fig 1 H K I, Please revise the word “exprssion” in the ordinate title.
Furthermore, the resolution of the figures need to be improved, especially Fig 4C and Fig 5A
and B
Review for 10.1186/s12876-021-01929-9 (2021)

Title: The rs9953490 polymorphism of DAL-1 gene is associated with gastric cancer risk in the
Han population in Northeast China
Version: 1 Date: 09 Apr 2021
Reviewer's report:
The study of Wang H and Jiang Y et al. explores the putative association of six SNPs, falling
within the DAL-1 gene, with gastric cancer risk in the Han population. The work is concise, but
the design of the study is relatively poor and some information is missing.
For instance, it is not clear how the authors selected the target SNPs within the gene of interest.
According to what it’s written, they used just the allele frequency as a criterion, however, I doubt
that just six SNPs have a MAF higher than 5% in Chinese Han. Please, specify the additional
criteria you have used to select the SNPs (missense, protein-truncating variants, UTR and so on).
The main result is quite interesting: in the dominant model, the SNP rs9953490 seems associated
with GC within smokers, pointing toward a scenario where an interaction is working. The fact
that the significance is not maintained after adjustments may also depend on the covariates you
have used: you write that you have adjusted also for smoking status, which, in my opinion, it
does not make sense, since your analysis was restricted to smokers. Then you also used drinking
habits. However, smoking status is often correlated to drinking habits. It is, therefore, possible
that adjusting also for drinking status may abolish the significant signal you have found.
Anyway, a major problem of the work is that you have done a lot of statistical testing without
checking if your significant results resist multiple test correction. Surely, adding this information
to the work will increase the statistical strength of your results.
My last point is the interpretation of the biological mechanism through which the SNP interact
with the N3 status and TNM stage III. You claim that its location within a regulatory region may
decrease the expression or affect the promoter methylation status of the gene. However, you can
directly check this information in public databases, such as GTEx. Indeed, you could verify that
the presence of the variant influences the gene expression in different tissues.
Minor points:
- If possible, please specify the meaning of the acronyms the first time you use them.
- I have spotted a few grammar errors and some syntax issues. A careful re-examination of the
text is necessary.
- Line 90: dbSNP is the proper name of the database (not UCSC).
- Line 130: Additional file 1 seems to contain allelic counts and not frequencies.
Review for 10.1186/s12876-021-01929-9 (2021)

Title: The rs9953490 polymorphism of DAL-1 gene is associated with gastric cancer risk in the
Han population in Northeast China
Version: 1 Date: 22 Apr 2021
Reviewer's report:
Wang et al. aimed to investigate the DAL-1 polymorphisms with gastric cancer risk.
This is another in a series of publications on finding genetic variants associated with gastric
cancer risk. Although a population size included in the study is relatively decent, the study has
a number of inconsistencies that need to be clarified.
The SNP selection criteria are poorly defined and it is not clear what is the “function” of these
selected SNPs. Authors stated that these SNPs are potentially functional? On what assumption?
Which databases, browsers etc. were used for their selection? These should be clarified.
Authors clearly wrote that was no association between 5 SNPs with GC risk, however the
conclusion says something else. Similarly, the authors observed the association with TA+AA
genotype of rs9953490 before adjustment, however after adjustment this association was lost.
The authors observed association only in stratified analyses on significantly smaller population.
These should be clarified.
The same applies for LD chapter. I assume that LD should be one of the criterions for SNP
selection. It is not clear how the authors selected haplotypes and how they analyzed the risk
of GC.
No correction for multiple testing was applied. In case the statistical analyses were corrected for
multiple testing, part of the results will not appear as significant.
Patients were collected in 2016, so the question arises as to why the authors did not performed
associations of SNPs with survival.
Genotyping part is poorly written.
How the cut of 58 age was selected in the analysis?
Minor:
Row 170 significantly appeared twice
Review for 10.1186/s12876-021-01929-9 (2021)

Title: The rs9953490 polymorphism of DAL-1 gene is associated with gastric cancer risk in the
Han population in Northeast China
Version: 3 Date: 31 May 2021
Reviewer's report:
The authors have considerably improved the manuscript and answered my suggestions with
just two exceptions. The first was about the multiple test correction, where they use a poor
justification for its absence (the fact that another paper did not use it). In my opinion, the authors
are partially right in saying that Bonferroni is very strict when it comes to little cohorts. Anyway,
I think that a brief sentence about the results using the correction (or a column in the tables with
the adjusted p-value) could improve the clarity and the scientific integrity of the work.
The second point was the use of smoking status as a covariate in a model where you already
stratified for smoking status (if I have understood correctly), which results in an over-adjustment
possible abolishing significant associations (if any).
In summary, the revised version of the work is still simple and maybe too simplistic, but it
provides clear and concise results on the topic.
Review for 10.1186/s12876-021-01931-1 (2021)

Title: Helicobacter pylori infection in Iran: demographic, endoscopic and pathological factors
Version: 3 Date: 15 Mar 2021
Reviewer's report:
The authors conducted a cross-sectional study, and tried to compare the demographic,
endoscopic, and pathologic findings in patients with and without H. pylori infection in Iran.
However, the authors did not mention which criteria or guideline was used for the endoscopic,
histologic evaluation, which is the main outcome of the study. The methods section lacks lots
of essential components. They suggested that there were significant relationship between some
clinical factors and the presence of H. pylori infection, but this should be suggested with a
multivariate analysis, which is not performed in this study. In addition, some endoscopic findings
were different from previous knowledges (ulcers not more frequent in H. pylori group), which
was not adequately explained in the discussion section. Honestly, there seems to be nothing new
or important in what the authors are trying to show.
There are too many English grammar mistakes and typos. Tables and Figures need to be
reviewed and revised thoroughly.
Review for 10.1186/s12876-021-01931-1 (2021)

Title: Helicobacter pylori infection in Iran: demographic, endoscopic and pathological factors
Version: 3 Date: 09 Apr 2021
Reviewer:  Muinah Adenike Fowora
Reviewer's report:
This is an interesting study to add to the existing body knowledge on the factors that influence
H. pylori infection in patients with gastroduodenal disorders. The gap in information in the local
context of Iran makes this article adequate.
The following needs to be addressed in the study.
1. The methodology is insufficient to allow the study to be repeated in other areas.
The study design was not correctly mentioned. The authors wrote, "This study was conducted
as a questionnaire". The study, however, used a cross-sectional study design.
2. Pathology may not be sufficient to screen the patients for H. pylori infection. A brief
description of the pathological method used should be provided as well as the criteria for
positivity. I will recommend the use of direct detection of H. pylori from the collected biopsy
using molecular methods or serological methods.
3. The researchers used only descriptive statistics and chi-square analysis for their statistical
analysis. Considering that multiple variables were collected with the questionnaire. A chi-square
analysis may not be sufficient to analyze this data. They should consider using a multiple logistic
regression model.
4. There are several typographical and writing issues with the manuscript. I suggest the authors
used a writing editor to address this problem
Review for 10.1186/s12876-021-01931-1 (2021)

Title: Helicobacter pylori infection in Iran: demographic, endoscopic and pathological factors
Version: 4 Date: 25 Jun 2021
Reviewer:  Muinah Adenike Fowora
Reviewer's report:
Well done, and thank you very much for the revisions. A few things still need revision/
clarifications in the manuscript.
1. You mentioned that 'Diagnosis of H. pylori infection was established for all patients
using pathology' under the 'Patients' section of the materials and methods. Subsequently, you
mentioned under the 'Specimens' section that 'rapid urease test (RUT) was used for the diagnosis
of H. pylori infection in a specimen from the antrum'. This should be clarified and revised.
2. A multivariate analysis should be used for the statistical analysis. A brief description of this
should be included in the manuscript.
Review for 10.1186/s12876-021-01928-w (2021)

Title: A novel pN3 gastric cancer staging system with superior prognostic utility based upon
the examination of over 31 lymph nodes: a propensity score-matching analysis
Version: 1 Date: 21 Jun 2021
Reviewer's report:
By using the SEER database, the data of examined lymph nodes in patients with gastric cancer
were analyzed in this study and developed a novel TNM staging system for pN3 patients.
The results of study is important in survival evaluation and decision-making for pN3 patients
according different numbers of examined and metastatic lymph nodes. The statistic method in
present study was appropriate.
While high discrimination and calibration for their model was demonstrated, several minor
suggestions should be addressed here:
1. Why did the authors exclude patients with cardia cancers?
2. Why did pT3 and pT4a patients were analyzed together in the survival analyses shown in
Figure 4?
3. Although the number of examined lymph nodes is directed to be more than 15 at present, this
number is still insufficient in many cases. Please discuss this situation in the Discussion section.
4. N stages and T stages illustrated in Figure 4B-4F and Figure 5 should be exchanged into pN
stages and pT stages.
Review for 10.1186/s12876-021-01928-w (2021)

Title: A novel pN3 gastric cancer staging system with superior prognostic utility based upon
the examination of over 31 lymph nodes: a propensity score-matching analysis
Version: 1 Date: 24 Jul 2021
Reviewer:  Ju-li Lin
Reviewer's report:
In this study, pTxN3M0 GC patients from SEER database with advanced GC were selected to
evaluate the relationship between prognosis and the numbers of examined and metastatic lymph
nodes. The authors compared the prognosis of GC patients under different T stages according
to different numbers of examined lymph nodes, and optimized the original AJCC TNM staging
system. It was proved that the optimized novel TNM staging system had a better prognostic
assessment ability. At the same time, there are several deficiencies need to be improved in this
study#
1. Compared with the AJCC TNM staging system, the prognostic assessment advantage of the
novel TNM staging system did exist but is not significant. Please highlight the significance of
this study in the Discussion section.
2. Please clearly indicate which population was being analyzed in the specific survival curve
in Fig.3 and Fig.4.
3. What were the authors' principles for selecting clinicopathological features for PSM analysis?
4. I suggest the authors make a decision curve analysis to further evaluate the novel TNM staging
system for making clinical decision.
5. Finally, the English quality of the manuscript is mediocre and needs grammatical adjustments.
Review for 10.1186/s12876-021-01928-w (2021)

Title: A novel pN3 gastric cancer staging system with superior prognostic utility based upon
the examination of over 31 lymph nodes: a propensity score-matching analysis
Version: 3 Date: 28 Aug 2021
Reviewer:  Ju-li Lin
Reviewer's report:
No comment after review.
Review for 10.1186/s12876-021-01928-w (2021)

Title: A novel pN3 gastric cancer staging system with superior prognostic utility based upon
the examination of over 31 lymph nodes: a propensity score-matching analysis
Version: 3 Date: 10 Sep 2021
Reviewer's report:
The comments by the reviewer #1 Jingyu Deng were properly responded by the authors, and
the manuscript was revised accordingly.
Review for 10.1186/s12876-021-01930-2 (2021)

Title: The PSC Scientific Community Resource: An Asset for Multi-omics Interrogation of
Primary Sclerosing Cholangitis
Version: 1 Date: 20 Jul 2021
Reviewer's report:
In this study, Ali et al. seek to establish the new data sets of PSC patients and control individuals.
PSC is a rare disorder and it is important to facilitate PSC research by sharing data and samples
with researchers in basic science who has limited access to samples/tissues of PSC patients.
I do not have any major criticism for this manuscript except a few minor comments. PSC is
characterized by liver fibrosis, inflammation, and ductular reaction (bile duct hyperplasia). It
seems that the authors do not include these characteristics (e.g., fibrosis levels). Is there any
reason? Scientists may use shared tissue samples and analyze liver fibrosis levels. Is it possible
for other scientists to add another parameter in the dataset (e.g., fibrosis levels) and share data
with others (e.g., histological images for Sirius Red staining)? How do the authors make it?
Open the website/portal/cloud or something that approved users can access and edit/add data,
or do the authors do not want to do that way? I feel like that it is unclear how the authors share
datasets with researchers, how they expand, and how they use them.
Review for 10.1186/s12876-021-01930-2 (2021)

Title: The PSC Scientific Community Resource: An Asset for Multi-omics Interrogation of
Primary Sclerosing Cholangitis
Version: 1 Date: 21 Jul 2021
Reviewer's report:
Here, authors provide a new protocol (PSC Scientific Community Resource (PSC-SCR)) used
to facilitate the research in PSC with the goals of individualizing patient care and improving
patient outcomes. The study was performed very well and it covers in very detailed all the steps
that the partecipantes are required to do. However there are minor comments that the authors
should addressed:
Authors claim that the PSC/control participants are asked to fill out two questionare: the updated-
comprehensive questionare and food frequency questionare. Could authors provide a template
of the two questionnaires in the paper as well as could they clarified which is the difference
between the old and the update version of the comprehensive questionnaire?
Review for 10.1186/s12876-021-01921-3 (2021)

Title: Efficiency of Complete Omentectomy in Patients with Resectable Gastric Cancer: A
Meta#analysis and Systematic Review
Version: 0 Date: 30 Jul 2021
Reviewer:  Giuseppe Brisinda
Reviewer's report:
Extremely interesting work.
Always current topic.
Truly robust study selection and analysis of results.
Giuseppe Brisinda, MD
Review for 10.1186/s12876-021-01921-3 (2021)

Title: Efficiency of Complete Omentectomy in Patients with Resectable Gastric Cancer: A
Meta#analysis and Systematic Review
Version: 0 Date: 09 Aug 2021
Reviewer's report:
The authors analyzed the impact of complete omentectomy on the outcomes of patients with
resectable gastric cancer treated with radical gastrectomy.
The topic is extremely interesting and deserves to be further explored to provide evidence and
guidance for the treatment of gastric cancer.
The paper is interesting, well-written, and easy to read. It provides a well-conducted review of
the literature offering an interesting overview of this controversial topic. The aim of the study
is clearly stated.
A subgroup analysis of omentectomy in patients with cT3 or cT4 gastric cancers would have
been useful to provide data in support of CO or NCO. This represents a limitation of the study
but the authors were unable to perform a subgroup analysis since only a few studies focused on
the effect of CO in this subgroup of patients.
Challenging current practice with robust data leading to adequate treatment maintaining the
same oncological outcomes with less invasive procedures represents the direction to follow.
Review for 10.1186/s12876-021-01921-3 (2021)

Title: Efficiency of Complete Omentectomy in Patients with Resectable Gastric Cancer: A
Meta#analysis and Systematic Review
Version: 0 Date: 12 Aug 2021
Reviewer:  Phuuwadith Wattanachayakul
Reviewer's report:
This article is clearly written and well organized.
Review for 10.1186/s12876-021-01919-x (2021)

Title: Impact of dietary compositions and patterns on the prevalence of nonalcoholic fatty liver
disease in Japanese men: a cross-sectional study
Version: 1 Date: 02 Apr 2021
Reviewer:  Shahinul Alam
Reviewer's report:
Due to its cross section design, causal relationship between dietary pattern and NAFLD couldn't
be investigated.
Dietary, exercise and smoking behaviors were determined using self reported questionnaires,
which could be influenced by subject's biases including under and over reporting.
This is a small scale study.
Please justify the sample size.
Effect of confounding variables (exercise, seating time, sedentary life)were not removed. Table
3 is not good for understanding.
Review for 10.1186/s12876-021-01919-x (2021)

Title: Impact of dietary compositions and patterns on the prevalence of nonalcoholic fatty liver
disease in Japanese men: a cross-sectional study
Version: 1 Date: 20 May 2021
Reviewer:  Arjuna Priyadarshin De Silva
Reviewer's report:
This is an interesting article on an important topic. However, the most important finding of the
"washoku diet" seems that the consumption of mushrooms seems to be protective. The authors
need to elaborate on this why? what is the possible active ingredient? This may be the basis of
future treatment.
Review for 10.1186/s12876-021-01918-y (2021)

Title: Elevated tumor expression of Astroprincin (FAM171A1) is an independent marker of
poor prognosis in colon cancer
Version: 2 Date: 30 May 2021
Reviewer's report:
1.In the main text file author did not mention the figure number (the result of
immunohistochemistry figure 1 A-D) and there is no scale bar in the figure.
2. Author should show the adjacent normal area and tumor area in the same tissue sample that
will be good control.
3. I have a big concern about the expression of APCN protein expression in tumors.
The TCGA database (http://ualcan.path.uab.edu/cgi-bin/ualcan-res.pl) and protein ATLS
database (https://www.proteinatlas.org/ENSG00000148468-FAM171A1/pathology/colorectal
+cancer#ihc) show low expression of APCN/FAM171A1 protein and survival rate is more in
APCN upregulated cancer patient. however, in this study, it has been shown that APCN protein
is upregulated in advanced cancer.
however, there are some reports which support this study. The author should discuss these points
in the discussion section.
4. In the method section (immunohistochemistry) the author does not mention about blocking
step.
5. to analyze the specificity of the antibody author should use the peptide as a competitive
inhibitor.
6.author should analyze the expression of the EMT marker (fibronectin/vimentin) in genetically
modulated APCN protein by siRNA or shRNA in colon cancer cells (Caco2 cells/HT29 cells/
HCT116 cells)
7.In the background section it has been written as 700.000 deaths, it should be 700,000 deaths.
Review for 10.1186/s12876-021-01918-y (2021)

Title: Elevated tumor expression of Astroprincin (FAM171A1) is an independent marker of
poor prognosis in colon cancer
Version: 5 Date: 20 Jul 2021
Reviewer's report:
Kaprio et al have resubmitted their manuscript on the investigation of APCN in colon cancer. I
appreciate their response to my comments and concerns. In particular, I believe the manuscript
was strengthened by the now included supplementary data on patient information and the
additional analysis on Stage II data. I have three additional improvements that need to be made
that are described below (which should be easy for the authors to address).
1. Please correct the grammar in this sentence that was added to the introduction – it is
incomplete. “Translating biomarkers into clinical use is challenging, in addition to potential
biomarker also large enough patient series, validation series, analytical validation between
laboratories and prospective series in a later phase are needed.”
2. In Figure 1. The authors added a scale bar to Figure 1A, but an appropriate scale bar needs
to be added to every image.
3. Figure 1E was also added and described in the legend as “Colon cancer and tumor-next normal
epithelium” this is worded a bit odd. Perhaps simply “Normal epithelium neighboring a colon
tumor”.
Review for 10.1186/s12876-021-01918-y (2021)

Title: Elevated tumor expression of Astroprincin (FAM171A1) is an independent marker of
poor prognosis in colon cancer
Version: 5 Date: 25 Jul 2021
Reviewer's report:
The study seems not to have major methodological pitfalls. The manuscript is clear and parts
are quite balanced. excellent work and I will suggest it for publication.
Thanks,
Regards,
Balawant Kumar, Ph.D.
Instructor
Biochemistry and Molecular Biology
College of Medicine
University of Nebraska Medical Center Omaha NE
Review for 10.1186/s12876-021-01911-5 (2021)

Title: Mutation analysis of the ATP7B gene and genotype-phenotype correlation in Chinese
patients with Wilson disease
Version: 4 Date: 23 Jan 2021
Reviewer's report:
This is very interesting paper describing the genetic examination of large cohort of WD patients,
the authors described the frequency of different mutation, finding also new pathogenic variants.
and discussing the genotype-phenotype correlations I have a comment to the discussion section:
1) there are several papers describing the genetic studies in WD in different populations
(European, Korean, Irania, etc...) published, describing also significance of different mutations
quite recently, could you discuss them  e.g. Kluska, et al Whole-exome sequencing identifies
novel pathogenic variants across the ATP7B gene and some modifiers of Wilson's disease
phenotype. Liver Int 2019,   or reviews chapters describing genetic and epidemiology in
Handbook of Clinical Neurology 2017..  There are also several papers describing the effect of
different mutation in ATP7B
2) discussing genotype-phenotype correlation there are also several papers describing the effect
of type of mutation (frameshift, etc) on copper metabolism as well as phenotype presentation -
could You compare Your results with literature?
4) finally almost 20% patients were not confirmed genetically, how could You explain it? could
You compare it with data from other studies?
5) ten bibiliography should be updated on papers published in two-three years (several genetic
as well as epigenetic  studies were performed in WD as well as quite new review papers),
I recommend to accept this interesting paper after revision