JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-01764-y (2021)

Title: Correlation between the geographical origin of Helicobacter pylori homB-positive strains
and their clinical outcomes: a systematic review and meta-analysis
Version: 1 Date: 08 Feb 2021
Reviewer's report:
Meta-analysis enable us to assimilate data from a variety of sources and derive variability among
effect sizes, moderator variables and the mean and variance of underlying population effect from
the previous study results. There are six processes for conducting a meta-analysis study. The
first process of meta-analysis is doing a literature search. The authors performed a literature
search by using global databases such as Scopus, Web of Science, and PubMed to collect all
the studies relevant to the study’s purpose. Then the decision on some inclusion criteria and
applying them should be done. In the study, inclusion and exclusion criterias are defined. 138
related articles were collected and 126 articles were deleted according to inclusion criteria. In
addition, calculating effect sizes for each included study; doing the basic meta-analysis; doing
more advanced analysis like publication bias analysis and exploring moderator variables are the
next steps respectively. Random-effects model, and fixed-effects model are both used. The bias
is measured by using funnel plot and Egger’s test which  predicts discordance of results when
meta-analyses are compared with single large trials. The last process of meta-analysis is the
writing part of the overall results of the meta-analysis.
My concerns are listed below:
1- The statistical results are presented in the text. However I could not find average effect size
score. Is it reported? If not, why?
2- Studies have more balance under a random effects model. Under the fixed effects model,
larger studies share most of the total weight. Under the random effects model, extreme studies
is related to their sizes. If they are large, they lose their effects, whereas if they are small, they
gain influence. I could not find effect size and overall effect size based on random and fixed
effects model scores in the forest plots.
3- For statistical reporting, radial plot is also a good option to represent aggregate data.
4- Heterogeneity test results and publication bias are provided in the study. Did authors use
moderator analysis? If not, why? Moderating effects should be provided to represent information
about statistical difference in effect size.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 1 Date: 13 Dec 2020
Reviewer's report:
This an interesting and well written paper, but some issues should be addressed by the authors
1) Did the authors evaluate MELD score?
2) In Table 1 proportions % would be useful as well as to present the comparison between died
and alive pts
3) How did the authors manage liver transplantation in their analysis? Similarly, the therapeutic
manipulations of HCC?
4) How did the authors indetify the cut offs for each variable (e.g. AFP, gGT etc?) Why they
did not analyse these variables as continues?
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 1 Date: 24 Dec 2020
Reviewer's report:
The authors explored the mortality and HCC rates and associated risk factors in 1,412 Japanese
patients with decompensated hepatitis C virus-related cirrhosis. I have some comments.
1.Please add the flow chart of patients selection.
2.Could you add the risk factors for HCC? Because, in patients with decompensated liver
cirrhosis, clarifying the risk factors of HCC can help identify high-risk patients, which may be
beneficial to individualized management of patients.
3. In Results of "Factors associated with mortality", the authors wrote "The parameters
(e.g., ascites, hepatic encephalopathy, esophageal varices, albumin, total bilirubin, creatinine,
ammonia, and prothrombin time) that strongly correlated with other parameters were considered
confounding factors and excluded from statistical analysis". Why excluded esophageal varices?
4. In Table 2, in univariate analysis, sex and AST are risk factors significantly related to mortality
(P<0.001 and P=0.0034). Why were they not included in the multivariate analysis?
5. The Discussion was poor organized and failed to explain or highlight the key findings of this
article.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 1 Date: 25 Dec 2020
Reviewer's report:
The authors performed a large study though the median follow up is rather limited (2 years).
However, the main issues with the study are (1) the lack of novelty since the natural history of
untreated HCC or decompensated liver disease in HCV patients have been well described and
(2) lack of clinical relevancy because the current practice is to treat these patients.  Data have
been overwhelming in regards to the high effectiveness and safety of DAA treatment for HCV
patients with decompensated liver disease including HCC. Thus, outcome data for untreated
patients are no longer clinically relevant.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 2 Date: 19 Jan 2021
Reviewer's report:
Thank you for your response, my comments have been well answered. But I still have a small
question, the authors replied that they have included esophageal varices as a parameter in the
present statistical analysis. However, as shown in Tables 2 and 3, I did not find the factor of
"esophageal varices" in the univariate analysis.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 2 Date: 30 Jan 2021
Reviewer's report:
The paper has been improved. Although i recognize that the authors managed to reply properly
in most of the issues, some limitations still remained, such as MELD score
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 2 Date: 01 Feb 2021
Reviewer's report:
This article explored the association of decompensated hepatitis C virus-related cirrhosis with
mortality rates and risk factors in 1,412 Japanese patients. Some comments are listed.
Tables and Figures section:
1. The authors mentioned that they were only able to evaluate PT-INR in this study in 60% of
all cases, therefore the number of patients who evaluate the laboratory tests should be listed in
the Table 1 in order to make the meaning explicitly.
2. The words “difficult to follow-up” should be revised as “lost to follow-up” in Figure legends.
3. In the last revision, the review had proposed that “sex” and “AST” in Table 2 was not included
in multiple factors, but the author didn’t give a convincing explanation. P values are indeed
<0.05.
Discussion section:
1. The authors emphasized that “This study shows that these patients have a favorable prognosis,
possibly due to symptomatic treatment.” in line 226-227, but there was not mentioned of
treatments in the original text, which hardly draw such the conclusion reasonably. The reason
is not explained in detail, which could be elaborated.
2. The words “In Japan, the most common cause of death is liver cancer.” in line 238-239 should
be supported by some references.
3. The Editor and Reviewers have raised questions about the importance of drug therapy and
MELD score in the last revision. If the author could not resolve these questions, it could be
explained in the Limitation Section. The words mentioned in the Response to the Reviewers
Letter that “Most of the HCC treatments for decompensated cirrhosis are TACE, but there are
some old cases and details are not available.” could be mentioned in the original text to explain
the limitation of drug therapy.
4. The information was confusing when talking about the parts marked in red, such as the words
“Liver transplant cases were not included in this study.” in line 263-264 were illogical in the
context.
5. The associated independent risk factors such as low estimated glomerular filtration rate, low
serum sodium level, low platelet count, and high #-glutamyl transferase and #-fetoprotein levels
(all patients) could be explained the relationship with the prognosis of decompensated HCV-
related cirrhosis in the Discussion.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 2 Date: 13 Feb 2021
Reviewer's report:
1. The role of treatment for viral hepatitis C (HCV) infection on mortality should be presented
and discussed. What are The mortality rate and hepatocellular carcinoma (HCC) rate among
those having DAA or other treatments with sustained response, treatment without sustained
response and no treatment?
2. The role of treatment for HCC on mortality should be presented and discussed.
What are the mortality rate among those with curative treatment, palliative treatment and
supportive treatment only?
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 2 Date: 19 Feb 2021
Reviewer's report:
This study was performed focusing on the long-term prognosis of hepatitis C-related liver
cirrhosis.
However, multivariate analysis did not show any new findings related to survival. Most of the
parameters are well-known factors for poor prognosis. Hence, the authors need to search for a
new prognostic model to predict the patients’ outcomes. Another problem is that information
regarding the HCC stage and treatment is lacking. If the authors do not want to exclude patients
with HCC, they need to provide such data.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 5 Date: 21 Mar 2021
Reviewer's report:
Thanks for the responses, most of my comments have been well answered. But I still have a
few questions.
1. Although neither “sex” nor “AST” was extracted as a significant factor in the multivariate
analyses, the specific P-values should be list in the Table 2.
2. Authors have already added the description of symptomatic treatments in the Discussion
section (Page 10, lines 208-215), and it should be more reasonable if these words are moved
to Result section.
3. Authors have revised the words that “In our results, the eGFR and serum sodium level
were important factors as components of the MELD score. Platelets reflect the degree of liver
fibrosis. The AFP level reflects not only liver cancer, but also severe inflammation and fibrosis
progression.” (page 12, lines 255-258), and these words should be supported by some references
and further improved.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 5 Date: 21 Mar 2021
Reviewer's report:
According to the authors' response, anti-viral therapy and hepatocellular do affect the survival
rates. But, the case number are too small to be presented as figures. Instead, these results are
stated and explained in discussion.  It is acceptable.
Review for 10.1186/s12876-021-01770-0 (2021)

Title: Mortality rates and risk factors in 1,412 Japanese patients with decompensated hepatitis
C virus-related cirrhosis: A retrospective long-term cohort study
Version: 5 Date: 26 Mar 2021
Reviewer's report:
Thank you for your reply. My comments have been answered, and I have no other comments.
Review for 10.1186/s12876-021-01771-z (2021)

Title: Cost-effectiveness of TAS-102 plus bevacizumab versus TAS-102 monotherapy in
patients with metastatic colorectal cancer
Version: 0 Date: 15 Feb 2021
Reviewer's report:
The authors conducted analysis regarding treatment cost effectiveness of TAS-102 plus
bevacizumab in advanced CRC. This regimen was investigated in phase 2 study only and
showed promising activity.  Determining cost effectiveness of new regimens, especially those
not supported by phase 3 data, is an important exercise. The study is well conducted. Methods are
well outlined and rationale for certain parameters chosen in analysis is explained. The authors
also have a nice discussion about the limitations of this study and how it relates to costs and
similar analysis in other countries.
Review for 10.1186/s12876-021-01772-y (2021)

Title: Cholelithiasis and Cholecystitis in Children and Adolescents: does this increasing
diagnosis require a common guideline for pediatricians and pediatric surgeons?
Version: 1 Date: 18 Jan 2021
Reviewer:  Craig A. Friesen
Reviewer's report:
This is a well designed study which presents novel and interesting data. I particularly appreciate
the inclusion of 2 different methods of assessment that are complementary. I only have two
comments both of which should be considered quite minor.
1. The phrase "showed a certain insecurity" (last paragraph on pg. 11) is curious and the intent
not clear to me.
2. The authors call for the development of evidence-based pediatric guidelines" (last paragraph
on pg. 13)- it would be of interest  for the authors to lay out their ideas of what evidence is
lacking and what questions still need to be answered in order to develop such guidelines.
Review for 10.1186/s12876-021-01772-y (2021)

Title: Cholelithiasis and Cholecystitis in Children and Adolescents: does this increasing
diagnosis require a common guideline for pediatricians and pediatric surgeons?
Version: 3 Date: 04 Mar 2021
Reviewer:  Craig A. Friesen
Reviewer's report:
The reviewer concerns have been well addressed.
Review for 10.1186/s12876-021-01772-y (2021)

Title: Cholelithiasis and Cholecystitis in Children and Adolescents: does this increasing
diagnosis require a common guideline for pediatricians and pediatric surgeons?
Version: 3 Date: 21 Mar 2021
Reviewer's report:
Thank you for addressing the raised comments. Some methodological issues remain and not all
comment are  fully addressed.
Results
Not weight or length separately but only BMI can be reported for those under 18 years; Also
report the number of children with obesity according to BMI percentile (only % of overweight
now mentioned)
Influence of different case mix of complicated and uncomplicated cases in table 2 and kind of
complications complications (cystitis, cholangitis, pancreatitis, cholestasis, colics…) and table
3 should be reported and its influence discussed in the discussion section.
Figure 3 and its added description still leaves several questions open: What is the role of MRCP
and endosonography in case of US proven choldocholithiasis; what is the evidence of fasting
(none I am aware of): in which case antibiotics should be administered (my opinion: only in
case of changitis and should prompt rapid ERCP/cholecystectomy) ; diagnostics for pancreatitis
is missing
Discussion section:
Still a lack of detail on limitations/quality of the studies that are referred to: Important to mention
particularly a ‘high risk of selection bias‘
Limitations:
the added phrase is not clear enough: ‘’The study’s approach was chosen from the therapeutic
endpoint of cholecystectomy, which influences the selection of patients (bias) and might
therefore have an impact on the findings of the presented data ‘’  No conclusions can be made
on the risk benefit of a an expectant management as successful cases who do not undergo
cystectomy especially in asymptomatic cases can not be established.
Review for 10.1186/s12876-021-01765-x (2021)

Title: Sequential Transarterial Chemoembolization and Early Radiofrequency Ablation
Improves Clinical Outcomes for Early-intermediate Hepatocellular Carcinoma in a 10-year
Single-center Comparative Study
Version: 3 Date: 17 Dec 2020
Reviewer's report:
-The manuscript is generally well written.
-The methodology described is sound and the conclusions obtained from the data are
appropriately stated.
-Questions:
*1. (page 5, line 110) What was the tumor size limitation of the patients who were included, it
should be specified in the including criterion.
*2. (page 6, line 115) What was the definition of hemorrhagic risk ? Was it defined by INR or
platelets? should be stated clearly.
*3. (page 6, line 128) “The dosage of lipiodol and doxorubicin hydrochloride was determined
according to the tumor’s size and vascularity, and the patient’s underlying liver function”. How
was the dosage of lipiodol and doxorubicin be determined by liver function? it should better
be quantified.
*4. (page 8, line 162) When was the palliative TACE identified intolerable? Was the palliative
TACE continued to be performed when it failed to control tumor progression? Was other therapy
used after progression?
*5. The 95%CI of median OS (page 10, line 203) and (line 209) median OS should be provided
in the session of Result.
*6. (page 11, line 235) The reasons why some patients failed to receive combination therapy
within two weeks may be specified and discussed.
Review for 10.1186/s12876-021-01765-x (2021)

Title: Sequential Transarterial Chemoembolization and Early Radiofrequency Ablation
Improves Clinical Outcomes for Early-intermediate Hepatocellular Carcinoma in a 10-year
Single-center Comparative Study
Version: 3 Date: 20 Dec 2020
Reviewer's report:
This retrospective study investigated early RFA (TACE+eRFA) in 96 patients vs. 34 patients
with late RFA(TACE+lRFA) (1-2 TACE before RFA). The results showed a significant
difference of mOS (46 months vs 33 months; P < 0.001)#mTTP (28 months vs 14 months; P
#0.00)#ORR (89.6% vs 61.8%, P=0.000) and DCR (94.8% vs 73.5% P=0.002) between two
groups. Multivariable analysis showed that BCLC stage was an independent risk factor for OS
(P=0.038).
The study is important for clear demonstration that early RFA after TACE will have better
outcomes compared with RFA after 1-2 sessions of RFA.
Minor comments
1. The time of RFA after TACE was dependent on the disappearance of syndrome after
embolization and the recovery of liver function. Please provide the mean, median and range of
interval between RFA and TACE.
2. The TACE+ late RFA group is defined as received 1-2 TACE before RFA, then combined
with RFA treatment. Please provide the interval between two TACE and the proportion of one
or two TACE. Why define 1 or 2 TACE, on demand or 2 TACE as routine practice.
3. Please provide more detailed baseline characteristics between two groups regarding tumor
number and maximal tumor size. Since BCLC stage B has wide heterogeneity, the B1 or B2
may have different outcomes.
Review for 10.1186/s12876-021-01765-x (2021)

Title: Sequential Transarterial Chemoembolization and Early Radiofrequency Ablation
Improves Clinical Outcomes for Early-intermediate Hepatocellular Carcinoma in a 10-year
Single-center Comparative Study
Version: 7 Date: 31 Jan 2021
Reviewer's report:
none
Review for 10.1186/s12876-021-01765-x (2021)

Title: Sequential Transarterial Chemoembolization and Early Radiofrequency Ablation
Improves Clinical Outcomes for Early-intermediate Hepatocellular Carcinoma in a 10-year
Single-center Comparative Study
Version: 7 Date: 13 Feb 2021
Reviewer's report:
This manuscript has been significantly improved.
The authors did a good job of reviewing the paper  based on the suggestions given in my previous
review.
This work is now worthy of publication in BMC Gastroenterology.
Review for 10.1186/s12876-021-01765-x (2021)

Title: Sequential Transarterial Chemoembolization and Early Radiofrequency Ablation
Improves Clinical Outcomes for Early-intermediate Hepatocellular Carcinoma in a 10-year
Single-center Comparative Study
Version: 7 Date: 18 Feb 2021
Reviewer's report:
This article is dedicated to exploring the impact of the timing of TACE and RFA combined
therapy on the long-term efficacy of hepatocellular carcinoma patients, including overall
survival, tumor progression time, tumor response rate, and major complication rates. In this
article, HCC patients treated with initial TACE combined with RFA are apt to obtain long-term
survival. Even though the sample size of the study is limited, it also provides clinical evidence
for the timing of treatment for HCC patients, which is innovative.
Review for 10.1186/s12876-021-01750-4 (2021)

Title: Identifying potential biomarkers of nonalcoholic fatty liver disease via genome-wide
analysis of copy number variation
Version: 2 Date: 12 Dec 2020
Reviewer's report:
In this original manuscript, the authors assessed the contribution of CNV to the evaluation of
NAFLD in by a case-control study. They used high-density comparative genomic hybridisation
microarrays (ACGH) to analyse CNV on 12 NAFLD patients and 12 healthy controls. They
found CNVs involving nine genes may be associated with the pathogenesis of NAFLD
progression. The manuscript does contain some interesting data, however, there are several
concerns should be addressed before it can be considered for publication.
1. In this study, ACGH was performed in peripheral blood samples. However, some CNV
variation only in liver or some (lipid metabolism) genes only expression in liver regulating
NAFLD development which cannot be detected in blood samples. It is important to validate or
perform the study in liver samples.
2. The number of cases enrolled is small.
3. Liver biopsy is the gold standard test for diagnosis, grading, and histological assessment of
NAFLD. The findings in this manuscript should be confirmed in the samples diagnosed by liver
biopsy.
4. Since genomic CNV data was presented by pair, which means selected matched control has
a great influence on the result. The authors should give detailed eligibility criteria for control.
5. Does the expression of NLRP4 correlate to the NAFLD grade? Does the expression of nine
(CNV regions) genes correlate to the NAFLD grade?
6. The authors presented a lot of data about the length of CNVs. What does those data contribute
to assess CNV of NAFLD? Does different size affect gene expression of NAFLD grade?
7. The authors mentioned “based on liver fatty accumulation diagnosed by abdominal
ultrasound, NAFLD was divided into three grades, and four cases were selected from each
grade.” What is the detailed division of each grade?
8. In the clinical characteristics of NAFLD patients, did the authors measure free fatty acids
levels?
9. The authors mentioned NLRP4 gene participate in inflammatory responses and is a
variation gene.  The 12 ACGH samples and 557 validation samples are simple steatosis or
including NSAH? The author should give detailed patient information. The grade and clinical
characteristics of samples should be showed in Table V.
Review for 10.1186/s12876-021-01750-4 (2021)

Title: Identifying potential biomarkers of nonalcoholic fatty liver disease via genome-wide
analysis of copy number variation
Version: 2 Date: 04 Jan 2021
Reviewer's report:
The manuscript discusses  some key genes involved in the metabolism which came up in the
analyses. However, except referring to some existing literature, the authors didn’t substantiate
the findings with a probable signaling pathway that might be related to the gene  and gene
products identified.
The authors explained why the CNVs from the sex chromosomes were excluded. However,
information from that data could have explained a sex-based severity or risk factor of NAFLD.
The result of CNV study could have been validated with the actual gene expression analyses
from the CNV regions from the cases and controls and presented a graph (potentially a volcano
plot) making the study more convincing
Review for 10.1186/s12876-021-01750-4 (2021)

Title: Identifying potential biomarkers of nonalcoholic fatty liver disease via genome-wide
analysis of copy number variation
Version: 5 Date: 14 Feb 2021
Reviewer's report:
The study aimed to identify risk factors of NAFLD by genome wide CNV can can add significant
finding to the field. However, there are some fundamental issues that wasn't resolved through
the revision.
There wasn't any data from liver biopsies supporting the claim made by the genome wide
CNV analyses from peripheral blood. Such claims much be substantiated with data that directly
addresses the rationale of the study.  obtaining liver biopsies can be invasive but might be
essential in addressing the particular question that was being asked in this study.
A heat map was included in the revised manuscript. However, neither there were any explanation
( highlighted in red) in the discussion nor there were sufficient annotation. Thus even though
the heat map was included, it didn't add to the substance and understanding of the readers.
According to the manuscript figures, there were 63 losses and gains identified in the Y
chromosome. thus there was a huge impact from the sex chromosome which was excluded from
the study.
Review for 10.1186/s12876-021-01750-4 (2021)

Title: Identifying potential biomarkers of nonalcoholic fatty liver disease via genome-wide
analysis of copy number variation
Version: 5 Date: 15 Feb 2021
Reviewer's report:
In the revised version of the manuscript, the authors have responded some comments and added
some new data. However, the authors did not address the comments appropriate.
1. To reply reviewer 1 comment 1, the authors stated that the results in peripheral blood samples
may be more representative. The authors should explain why peripheral blood samples may be
more representative.
2.  Why did the authors present CNV data was by pair? The authors mentioned that NAFLD
was divided into three grades. Does the CNV significant different between different grades?
3. To reply reviewer 1 comment 7. The authors did not answer the principle of grade division.
4. The Figures are rough. Missing Y-axis labels in Figure1and 3 and missing all the labels in
heatmap.
5. The paper should be extensively revised to avoid grammar errors, typos and description
inaccuracy.
Review for 10.1186/s12876-021-01750-4 (2021)

Title: Identifying potential biomarkers of nonalcoholic fatty liver disease via genome-wide
analysis of copy number variation
Version: 6 Date: 26 Mar 2021
Reviewer's report:
The comments of the reviewers were addressed by the authors in the revised manuscript.
The authors explained the issues raised by the reviewers and explained the limitations of this
study.
No further revisions/comments on the manuscript.
Review for 10.1186/s12876-021-01748-y (2021)

Title: Relationship between body composition and the histology of non-alcoholic fatty liver
disease: a cross-sectional study
Version: 3 Date: 09 Feb 2021
Reviewer's report:
In this manuscript, the authors examined the relationship between body composition and non-
alcoholic fatty liver disease progression as indicated by fibrosis and the non-alcoholic fatty liver
disease activity score. The authors found that fibrosis in non-alcoholic fatty liver disease, an
indicator of unfavorable long-term outcomes, is associated with more indices of fat mass than
of those of muscle mass. The manuscript does contain some interesting data, however, there are
several concerns should be addressed before it can be considered for publication.
1. The authors stated that no studies have compared the contributions of fat mass and muscle
mass to NAFLD histology. However, the effect of body composition on the liver function has
been determined (PMID: 29948305).  In general, this paper is too related to the published one
which greatly diminishes enthusiasm for the findings.
2. What is the muscle mass/ht2 to fat mass /ht2 ratio according to the stage of fibrosis?
3. The number of the patients should be increased.
4. In Additional file 1, the authors showed that muscle mass/ ht2 was increased with steatosis
grade. This data should be confirmed with more cases.
5. In Additional file 2, the authors showed that there were no significant differences of body
composition in lobular inflammation grade. However, there were significant differences of body
composition in the stage of fibrosis. The data should be confirmed with high number cases, since
inflammation is key to drive NAFLD to NASH (with fibrosis). Did the author investigate the
correlation between fibrosis and lobular inflammation, fibrosis and body composition, lobular
inflammation and body composition?
6. What is normal muscle mass/ht2 median? Compared to normal, the muscle mass/ht2 in
NAFLD was increased or decreased?
7. It will be better also show normal human body composition to better distinguish body
composition changes in NAFLD.
8. Some statements are not accuracy. For example, the author stated that “There were no
significant differences in the lobular inflammation grade or ballooning grade between these
groups (Additional files 2 and 3)”. It should be “in different lobular inflammation grade, there
were no significant differences in body composition”.
Review for 10.1186/s12876-021-01748-y (2021)

Title: Relationship between body composition and the histology of non-alcoholic fatty liver
disease: a cross-sectional study
Version: 3 Date: 11 Feb 2021
Reviewer:  Victoria Meadows
Reviewer's report:
The authors provide a needed investigation into the relationship between body composition (fat
mass and muscle mass), hepatic fibrosis, and NAS score/NAFL progression. The manuscript
presents limitations with patient diversity in this study, but lends evidence to the theory that
fat mass is indicative of liver steatosis and fibrosis the field of NAFL. Despite presenting
novel information, there are some issues that must be addressed before this manuscript can be
considered for publication:
- There was no threshold used to determine if patients in this study were clinically overweight
or obese. The authors should consider detailing the reasons for excluding organization of the
patients by BMI.
- The authors claim that this is the first investigation of  muscle mass and fat mass effect on
NAFL, but a few manuscripts have been published that look into this hypothesis, with alternate
methods. The authors should read over these publication and consider the relevance to their work
(supportive or not) PMID: 33562473, 33424768, 33535004, 33164304. These may help increase
the clinical impact of this study since the cohorts may be from different races and countries.
The discussion overall should include more recent publications that investigate the relationship
between muscle mass, fat mass, and/or NAFL stage, since many are previous to 2017.
- This manuscript would greatly benefit from publication of histological images that demonstrate
the results in this study. However, this can be ignored if the proper permissions cannot be
obtained.
- The authors may want to consider correlation analysis between fat/ht^2, fibrosis and NAS
score. This may provide a tool for clinicians to assess NAFL to NASH risk early in patient
diagnosis.
- The authors analyzed HbA1c levels, which may provide insight into the development of
insulin resistance in NAFL patients that are not yet diabetic. This might be an interesting future
direction, or expansion of the current manuscript, to increase clinical impact.
Review for 10.1186/s12876-021-01748-y (2021)

Title: Relationship between body composition and the histology of non-alcoholic fatty liver
disease: a cross-sectional study
Version: 5 Date: 29 Mar 2021
Reviewer:  Victoria Meadows
Reviewer's report:
The authors addressed the concerns of this reviewer with great detail and have indeed expanded
on their previous manuscript.
Review for 10.1186/s12876-021-01757-x (2021)

Title: Perioperative risk factors for survival outcomes in elective colorectal cancer surgery: A
retrospective cohort study
Version: 6 Date: 30 Mar 2021
Reviewer:  Dario Parini
Reviewer's report:
Dear Authors,
I really appreciated to read your study and to have the possibility to review it.
Is very interesting to read about relation between inflammation status, inhalation anesthesia and
survival outcomes.
I have some considerations to submit to you:
1. In your analysis, you didn’t consider, between risk factors for long-term survival, surgical
complications, above all anastomotic leak, that is known to worse oncologic outcomes.
2. Similarly, you didn’t consider adjuvant chemotherapy, an other important factor in
determining long-term oncologic outcomes.
3. An other factor that you didn’t analyze is budding, an histological characteristic more and
more important in predict oncologic outcomes.
Would you be able to add these 3 factors in your statistical analysis? Anastomotic leak, in
particular, is a peri-operative risk factor that I think has to be considered
4. Why did you use Inflammation Prognostic Score (IPS) as inflammation grading and not other
scores, for example Glasgow Prognostic Score (GPS), a validated and easier to calculate score?
5. When you consider inflammatory cell response, you use Klintrup–Makinen score: is this
grading system the most diffused? Could you add references about that?
Thanks for the answers you will be able to give
Review for 10.1186/s12876-021-01747-z (2021)

Title: Golimumab improves work productivity in patients suffering from moderate to severe
ulcerative colitis: results of a prospective study over 24 months.
Version: 3 Date: 22 Feb 2021
Reviewer:  Sami Hoque
Reviewer's report:
Please revise the English in the result section in the abstract to make it clear for the reader.
Review for 10.1186/s12876-021-01747-z (2021)

Title: Golimumab improves work productivity in patients suffering from moderate to severe
ulcerative colitis: results of a prospective study over 24 months.
Version: 3 Date: 23 Feb 2021
Reviewer's report:
I think the study is useful and answers the initial question. It is especially interesting to have
a two-year follow-up and to see that personal and health matters both improve progressively.
There are only two remarks I have to make. First of all, there are so many abbreviations that
it is hard to follow and you have to keep going back and forth to understand what each one
stands for. And, secondly, a sentence speculating on why there is such a high withdrawal of
informed consent would be appropriate, because there is no intervention and the reader wonders
why patients have withdrawn, and if that has influenced the results.
Review for 10.1186/s12876-021-01751-3 (2021)

Title: Clinicopathological and prognostic evaluations of anorectal cancer after fecal diversion
for patients with Crohn's disease
Version: 2 Date: 05 Mar 2021
Reviewer:  Weiming Zhu
Reviewer's report:
the topic of this paper is interesting, the authors reviewed the 1615 CD patients and found 232
patients with diverted stomas, among which 10 patients suffered from anorectal cancers and
received APR. and the authors emphasis the importance of surveillance in CD patients after
diversion.
The following points should be clarified:
1 In the “Methods” of the abstract, the authors stated that “Patients diagnosed with anorectal
cancer following fecal diversion were identified”, but in the text, there were also 31 anorectal
cancer patients in the non-diverted group were matched , and in the diverted group, the number
of patients were 12 in the “Results” paragraph but 11 in the text. I’m not certain if the 31 patients
were CD patients in the 1615 patients group, or from other groups.
2 The paper described the result of the 10 patients undergoing abdominoperineal resection, but
the rest one among the 11 patients were not given.
3 The authors classified the location of cancer as anorectal and perianal fistula, but from the
histopathology, the perianal fistula originated cancer are also adenocarcimoma. Is it meaningful
to classify the cancer simply by location?
4 “heavy iron therapy”in Table 2 need simple description. Tumor site percentage are not shown
in Table 3.
Review for 10.1186/s12876-021-01751-3 (2021)

Title: Clinicopathological and prognostic evaluations of anorectal cancer after fecal diversion
for patients with Crohn's disease
Version: 2 Date: 06 Mar 2021
Reviewer:  Y. Li
Reviewer's report:
Clinically, diagnosis pf anorectal cancer associated with Crohn's disease following fecal
diversion is often delayed, this leads to the poor outcome. The study by Kuroki et al. is
excellent and the author should be congratulated for their contribution. Identifying risks factors
of anorectal cancer in these Crohn’s patients with fecal diversion has clinical implications.
Therefore, potential risk factors including disease duration, duration of fecal diversion, medical
history, family history, etc. should be considered and performed in the study, both in the
univariate and multivariate analysis.
Review for 10.1186/s12876-021-01742-4 (2021)

Title: Chemotherapy alone vs definitive concurrent chemoradiotherapy for cT4b esophageal
squamous cell carcinoma: a population based study
Version: 2 Date: 22 Feb 2021
Reviewer's report:
The study by Chien et al addresses an interesting clinical issue: whether Chemotherapy or
radiochemotherapy is the most appropriate treatment for T4bM0 esophageal SCC and this was
studied in a relatively large population. However I suggest several revisions:
General:
English grammar and style should be improved. The text is written in the past, but should be
in the present time, i.e. "esophageal cancer was one of the leading..." schould be "....is one of
the leading...." etc.
Only survival data are analysed. Were grade 3-4 toxicity data not available? Since complications
are a concern of radiotherapy, the incidence of severe toxicity (fistula) is an important aspect
for interpretation of the survival results
Specific:
stick to  mentioning group C/T and group dCCRT, and not group A and B.
Methods: What do the authors mean by "excluding multiple treatment records" and by
"inclusion criteria modified from a relevant ongoing trial". I suggest to explain the exact in and
exclusion criteria.
a subheading is called Study population and intervention. But there is no intervention. I suggest
to skip the word "intervention"
Please mention the factors that were weighted for PS and PSW
Results,
A lot of covariates were analysed, but their impact was not mentioned in the text.
Primary analysis: "what do the authors mean by "the observed HR of 0.36...... could be explained
by an unmeasured confounder.........but weaker confoundering could not do so". This sentence
is unclear to me.
Discussion:
the authors state that the study relieved the concern in using radiotherapy. However no data on
toxicity of radiotherapy were mentioned.
A strong confounding factor is the unability to discriminate whether a patient has had  neo
adjuvant chemotherapy (nCT) or not. More data on the use of nCT, and discussion on the
potential selection bias by the response on nCT will improve the manuscript and the strength
of the main message.
Review for 10.1186/s12876-021-01742-4 (2021)

Title: Chemotherapy alone vs definitive concurrent chemoradiotherapy for cT4b esophageal
squamous cell carcinoma: a population based study
Version: 2 Date: 27 Feb 2021
Reviewer's report:
This is a thorough review of Taiwan registry data and the authors should be congratulated on
the lengths they have gone to appropriately analyse the data
It is stated that median follow up in the results (study population) was just 7 months and it is
unclear why such a short time given the duration of the review (unless limited by death?)
Was there any data on complications of radiotherapy treatment (eg fistula, rupture aorta etc) and
if not specifically rates or death within 3 months of completing high dose RT?
I would recommend changing the language such that the tense is present, ie the guidelines
currently show xx rather than did show yy
Review for 10.1186/s12876-021-01742-4 (2021)

Title: Chemotherapy alone vs definitive concurrent chemoradiotherapy for cT4b esophageal
squamous cell carcinoma: a population based study
Version: 3 Date: 22 Mar 2021
Reviewer's report:
the point by point answers and subsequent corrections are sufficient for me to advise acceptance
of the manuscript
Review for 10.1186/s12876-021-01746-0 (2021)

Title: A rapid preliminary prediction model for intestinal necrosis in acute mesenteric ischemia:
a retrospective study
Version: 2 Date: 17 Feb 2021
Reviewer's report:
The authors provide an interesting study on a crucial outcome of mesenteric ischemia: intestinal
necrosis. Although retrospective, the sample population is rather large. However, presentation
of the results can be improved, as well as discussion on recent studies on the intestinal necrosis
outcome.
Here are my comments in detail:
- P3L9 : “other methods”, please specify. Notably, the authors could mention the recent
implementation of intestinal stroke centers providing 24/7 care of mesenteric ischemia (PMID
29776790 and PMID 25466834) and including antibiotics (PMID 30538292)
- P5L95: please specify whether all specimens were specifically reviewed in order to rule out
superficial necrosis and confirm full thickness small bowel wall necrosis. Or discuss in the
limitation paragraph
- Methods: please clarify how you constructed the score, what was the formula used for
calculation based on the logistic regression scores (intercept…
- Discussion : The authors omit to discuss several recent studies on predictors of intestinal
necrosis in AMI. Notably, numerous studies identified lactate levels as major and independent
biomarker of intestinal necrosis (PMID 31934635 and 31361977 and 31205904 and 28266590).
The authors should discuss why they could not study lactate in their study and how this stands
as a limitation. Further, they should open the discussion on recent interventions that have
shown to reduce the occurence of necrosis (improve diagnostic delays (PMID 33156109), oral
antibiotics (PMID 30538292), revascularization, intestinal stroke centers(PMID 29776790 and
PMID 25466834) and confront these novel practices to their past experience in their center and
how they and the readers could improve their management.
- Table1: Please provide percentages instead of ratios, Please clarify if intervention refers
to revascularization, Please discuss why patients operated on for necrosis are not offered
anticoagulation and intervention in your center.
- Table 3. Multivariate analysis should best be performed including variables associated with
necrosis in univariate analysis (for example, therapy variables, PT, Cr) or known risk factors for
necrosis (origin of AMI). Or explain why these variables were excluded from the final model.
Review for 10.1186/s12876-021-01746-0 (2021)

Title: A rapid preliminary prediction model for intestinal necrosis in acute mesenteric ischemia:
a retrospective study
Version: 5 Date: 10 Mar 2021
Reviewer's report:
The authors have made satisfactory efforts to improve the discussion of their manuscript.
However, I suggest some final improvements before acceptance.
- the title may specify this is a development stage of a prediction model
- the abstract's and manuscript's conclusion may be mitigated: the model's accuracy should be
validated in further studies.
- the methods and/or results/tables section should specify which variables were selected and
entered in the model, even if they were then excluded by the forward elimination. I find it still
unclear.
- throughout the manuscript and, especially the abstract, please specify the units used for
calculation for WBC and DDimers as they may differ across labs and countries.
Review for 10.1186/s12876-021-01729-1 (2021)

Title: Absent or impaired rectoanal inhibitory reflex as a diagnostic factor for high-grade (grade
III–V) rectal prolapse: a retrospective study
Version: 1 Date: 13 Jan 2021
Reviewer's report:
In this manuscript, Dr. Park and colleagues performed a retrospective analysis of patients
presenting to a tertiary care center with anorectal complaints (including fecal incontinence,
constipation, and anorectal discomfort) who underwent both anorectal manometry and
defecography. They found that an abnormal rectoanal inhibitory response (RAIR) was
associated with high-grade rectal prolapse (Grades III-V) according to the Oxford classification
—with an association that persisted after multivariable control. There was a significant trend of
a higher proportion of abnormal RAIR associated with increasing degree of prolapse.
MAJOR COMMENTS
1.   Since this is a retrospective study, the association between abnormal RAIR and prolapse was
presumably an exploratory endpoint—i.e. the authors did not set out to prove this in advance
but were looking at predictors of prolapse in a cohort with multiple measured parameters.
This is absolutely fine, but the Introduction adopts a tone assuming that this was the a. priori
assumption of the analysis. I think the Introduction would be improved by addressing the
gaps in our ability to diagnose prolapse without more unpleasant testing (defecography) with
acknowledgement that the authors were likely looking for all associations and that absent RAIR
was most compelling.
2.  The Abstract would benefit from increased detail in the Methods, for example the fact that
symptom report was included as part of each patient’s assessment.
3.  How was clinical data collected from patients? Were validated patient-reported outcomes
used or were the responses to clinical questions yes/no. It would be helpful to know which
questions were asked and how were symptoms graded (continuous scale, categorical, yes/no).
4.  There are 30 “outcomes” as part of this analysis (30 patients with high-grade prolapse). Thus,
the general rule for multivariable adjustment is no more than 3 variables should be adjusted for
(rule of 10s). The included model is likely over-adjusted.
5.  It would be helpful to have more detail about the ROC analysis used to determine cutoff
values for inclusion in the multivariable analysis. Why not include these variables as continuous
covariates?
6.  It would be nice to include a sensitivity and specificity for abnormal RAIR as a predictor of
high-grade prolapse (since these are not related to disease prevalence).  Looks like sensitivity
is about 63% and specificity 74%.
Review for 10.1186/s12876-021-01729-1 (2021)

Title: Absent or impaired rectoanal inhibitory reflex as a diagnostic factor for high-grade (grade
III–V) rectal prolapse: a retrospective study
Version: 1 Date: 03 Feb 2021
Reviewer's report:
Methods:
Maybe the name ‘abnormal RAIR’ is not the correct name since you do not see anything special
on the RAIR but only do not see a RAIR, or the RAIR does reduce the anal resting pressure less
than 25%. Alternative: ‘No or less effective RAIR’
Has been checked if the patients with an abnormal RAIR had ganglioncels? It happens that at
adult age Hirschsprung is being diagnosed for the first time.
The asymmetry of the anal sphincter measurement is extremely sensitive for accidental position
mistakes when measured. How was checked that this measured correctly?
Statistical analyses:
How was checked that data was normally distributed?
Discussion:
If also the low grade group did have an abnormal RAIR, how can the abnormal RAIR than help
to diagnose the high grade group?
There are many other reasons to have a low maximum squeezing pressure, how can this
parameter than be a predictor of high grade rectal prolapse?
The shorting MRP and MSP were used without first mentioning them. Be careful that everyone
can follow your story.
Reference:
Reference 40 is not correct mentioned