JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02354-2 (2022)

Title: Linoleic acid pathway disturbance contributing to potential cancerization of intrahepatic
bile duct stones into intrahepatic cholangiocarcinoma
Version: 0 Date: 02 Apr 2022
Reviewer's report:
This research work is a study of intrahepatic cholangiocarcinoma (ICC) and intrahepatic bile
duct stones (IBDS) using GC-MS based metabolomics study on the pathological tissue. I
appreciate your research rationale and method used in this study. You propose that the linoleic
acid pathway may play role in cholangiocarcinoma carcinogenesis.
I have questions and comments as follows.
Major issues:
1. It's not clear about tissue representative, how do you select and confirm representative areas
for ICC tumor tissue, para-carcinoma tissue, and IBDS pathological tissue for study? Did the
authors confirm the tissue samples, ICC and IBDS cases, with pathologists in the specimens
selected for GC-MS?
2. Do you have any cases of ICC + IBDS in the same patient? How do you analyze them? If you
have that, the dataset could be analyzed in 5 subcategories; ICC tissue (cases without stones),
ICC tissue (cases ICC with IBDS), para-carcinoma bile duct tissue (cases ICC with IBDS), para-
carcinoma bile duct tissue (cases ICC without IBDS), and normal bile duct tissue (cases IBDS
without cancer).
3. Did you find any precancerous lesions like biliary intraepithelial neoplasia (BilIN) in your
cases? Is it present in para-carcinoma bile duct tissue?
4. Regrading exclusion criteria; "history of any metabolic diseases" should be defined more. Is
the list of metabolic diseases include obesity or dyslipidemia?
5. Regarding the surrogate marker for cholangiocarcinoma, the authors state GGT and AFP were
indicators of cancerization markers for hepatic carcinoma and disease characteristics of IBDS.
Could you please explain more and give some references.
6. Could you please explain the outlier of concentration of 9,12-octadecadienoic acid among
ICC-T.
Minor issues:
1. The word "metabonomics" in Scheme 1, is it correct?
2. The font sizes of (A) and (B) should be adjusted in Figure 2.
3. Also, the legend "ICC-L" in Figure 2 is not corresponding to the text.
Review for 10.1186/s12876-022-02354-2 (2022)

Title: Linoleic acid pathway disturbance contributing to potential cancerization of intrahepatic
bile duct stones into intrahepatic cholangiocarcinoma
Version: 0 Date: 14 Apr 2022
Reviewer's report:
In the present manuscript, Li, J., et al. first demonstrated the aberrant of linoleic acid pathway
in intrahepatic cholangiocarcinoma (ICC) and intrahepatic bile duct stone (IBDS). The levels
of total metabolites in ICC and IBDS were determined using GC-MS based metabolomics.
In addition, the correlation between key metabolite and clinical features of patients were also
investigated. The different pattern in in linoleic acid metabolism pathway between IBDS and
ICC were observed. The experiments were performed in a technically sound manner. The
overall idea presented has merit. This manuscript is good enough for publishing in BMC
Gastroenterology.
Review for 10.1186/s12876-022-02353-3 (2022)

Title: The Association between Dietary Inflammation Scores and Non-alcoholic Fatty Liver
Diseases in Iranian Adults
Version: 0 Date: 23 Feb 2022
Reviewer:  Nagisa Hara
Reviewer's report:
This paper discusses , the association of dietary inflammation scres (DIS) and empirical dietary
inflammatory patterns (EDIP) with the risk of nonalcoholic fatty liver diseases(NAFLD) in
Iranian adults. The main contribution of the paper is , dietary pattern with a higher score of DIS
and EDIP score , is related to an increased odds of NAFLD in Iranian adults.
This is an interesting observation that a dietary pattern with a higher score of DIS and EDIP
scores is a pro-inflammatory diet that is characterized by various unhealthy food choices.
I recommend that this paper be accepted.
However , there are some misrepresentations in some tables, so I suggest corrections.
Review for 10.1186/s12876-022-02303-z (2022)

Title: Population-specific cut-off points of fatty liver index: A study based on the National
Health and Nutrition Examination Survey data
Version: 1 Date: 29 Jan 2022
Reviewer's report:
GENERAL COMMENT
First proposed by Bedogni, Bellentani and Tiribelli in 2006 as an aid in selecting individuals
to submit to liver ultrasonography, over time, FLI has shown an amazing wider spectrum of
uses (Reviewed in https://mtodjournal.net/article/view/4410). In a recent reappraisal of FLI, the
above authors acknowledged the limitations of FLI, one of these being not having sex-specific
cut-off values.
SPECIFIC COMMENT
MAJOR
1. Introduction is too long and must be reworked aimed at focusing on FLI and the reserach
questions addressed here. In other words, I would suggest to summarize to a substantial extent
the section on NAFLD/MAFLD and rather illustrating the importance of  sex differences as a
research priority in NAFLD arena.
2. These Authors cite some outdated articles regarding accuracy of ultrasonography in the
detection of minor extents of steatosis: these studies were conducted when machinaries were
less sensitive and a re-evaluation has indeed led to completely different findings (https://
mtodjournal.net/article/view/4301) that must be discussed here.
3. I would also recommend to highlight that NAFLD/MAFLD is a heterogeneous condition and
that such heterogeneity underlies the development of precision medicine practices. The role, if
any, of FLI in this setting should be briefly discussed.
MINOR
1. GGT: gamma glutaryl transferase---> GLUTAMYL
2. Editing of English is recommeded
Review for 10.1186/s12876-022-02303-z (2022)

Title: Population-specific cut-off points of fatty liver index: A study based on the National
Health and Nutrition Examination Survey data
Version: 1 Date: 14 Feb 2022
Reviewer's report:
GENERAL COMMENT
This is an interesting study aiming at identifying cut-points of the fatty liver index (FLI) for the
general US population.
MAJOR COMMENTS
1. Please, note that – to have data which are truly representative of the US population using
NHANES – one has to consider its complex multistage probability design:
https://wwwn.cdc.gov/nchs/nhanes/continuousnhanes/Overview.aspx?BeginYear=2015.
Together with the exclusion of most subjects from the analysis (see below), the analyzed data
are unlikely to be representative of the whole US population. You can simply recognize this
limitation without the need of considering the complex multistage probability design.
2. 78% of NHANES 2017-2018 and 62% of NHANES III subjects were evaluated. Note that
NHANES researchers suggest handling missing data by multiple imputation. I am not asking
you to do that. I recommend that you recognize the limitations of this approach. It would
also be nice to have a paragraph in the Discussion addressing the limitations of the study, as
is generally requested by any research journal. A supplementary figure giving the number of
excluded subjects with the reason for exclusion would greatly increase – in my opinion – the
value of this manuscript. Furthermore, what do you mean with “invalid data”?
3. I am not a fan of the Youden index as a means to evaluate the accuracy of a diagnostic test.
The reason is that it gives the same weight to sensitivity and specificity and offers just one cut-
point. A diagnostic test is used at different cut-points to separately increase its sensitivity and
specificity, and there will always be a “gray zone” where no clinical decision can be taken.
For instance, the FLI was developed using two cut-points – which of course may vary from
population to population – with the aim of having values to “rule in” and “rule out” hepatic
steatosis. I am not asking you to perform a new analysis, but simply to defend your choice of
the Youden index.
4. Please recognize that a direct comparison of LUTE vs. conventional ultrasonography is not
possible here because they were performed in different NHANES samples. It is of course nice
to find that FLI performs reasonably well with a reportedly more accurate technique than that
with which it was developed.
MINOR COMMENTS
There are several typing and spelling errors. The paper should be checked by a mother-tongue.
Please report 95% confidence intervals for point estimates of prevalence of MAFLD.
P4 L2 I would not say that LUTE is “inexpensive”.
P10 L1 What do you mean by “dietary”.
P10 L13 NHANES data are not census data. See major comment #1 above.
P4 Note that sex was *not* a predictor of fatty liver in the FLI study and this is the reason why
it was not taken into account. Race could not be taken into account simply because all subjects
were Italian (Caucasian).
Review for 10.1186/s12876-022-02330-w (2022)

Title: On-site evaluation of pancreatic lessions according to Papanicolaou Society of
Pancreatobiliary Cytology, how can it contribute to diagnostic accuracy?
Version: 1 Date: 29 Mar 2022
Reviewer's report:
THe topic is interesting. I have the following comments:
1) The manuscript needs a deep grammar revision
2) References are not reported consistently. The journal guidelines should be strictly followed
3) I would add some comments on the great impact of the newer FNB needles in the field of
EUS-guided tissue sampling, citing the recent studies on the topic (PMID: 31374187; PMID:
35124072 ; PMID: 33390343)
Review for 10.1186/s12876-022-02330-w (2022)

Title: On-site evaluation of pancreatic lessions according to Papanicolaou Society of
Pancreatobiliary Cytology, how can it contribute to diagnostic accuracy?
Version: 1 Date: 01 Apr 2022
Reviewer's report:
This is a retrospective study investigating the role of rapid on-site evaluation during EUS-guided
fine-needle aspiration of pancreatic lesions. This topic has been extensively investigated in the
literature and different meta-analysis have been published.
In your study, it seems that you included all pancreatic biopsies during a timeframe of 6 years
(2016-2021). You included 162 procedures, which means 27 EUS-FNA per year. This means
that your is not a referral center, and this seems to be the most interesting point of your study.
In fact, most data already published come from tertiary high-volume centers. In the past, it was
postulated that ROSE can be of help in low-volume centers, but data in this setting are still
lacking.
I suggest reconsidering your manuscript in this view.
Specific comments are listed here:
1) English language must be extensively revised for grammar and typos by a native English
speaker.
2) Title should be changed. I suggest: “Impact of rapid on-site evaluation on diagnostic accuracy
of EUS-guided fine-needle aspiration of solid pancreatic lesions: experience from a low-volume
center”.
3) The primary aim should be to evaluate the impact of ROSE availability on diagnostic accuracy
of EUS-FNA of solid pancreatic lesions.
4) I suggest simplifying other aims. The number of slides is not important and is obviously
associated with the number of passes. You could evaluate the number of needle passes and the
adverse events with or without ROSE.
5) Methods: Any excluding criteria? For example, what about cystic lesions or solid/cystic
lesions? I suggest excluding purely cystic lesions.
6) Change “diagnostic ability” with diagnostic yield as reported in the AGA White paper (PMID:
29074447)
7) “Fujinon Fujifilm, Tokyo, Japan, VP-4450 HD, EG 580 UT” this is not a needle type
8) It is not clear what you mean by “non-ROSE group”. Indeed, in the “Technique” paragraph
the EUS-FNA procedure in the absence of ROSE is not described. Please clarify
9) It is surprising that the number of needle passes was higher with ROSE. Indeed, one of the
known advantages of ROSE. Which were the criteria to stop the procedure in the absence of
ROSE?
10) Simplify the results when talking about the Papanicolaou classification.
Review for 10.1186/s12876-022-02340-8 (2022)

Title: The relationships between IBS and perceptions of physical and mental health – a
Norwegian twin study
Version: 1 Date: 11 Feb 2022
Reviewer's report:
the self-health test is too synthetic a method to define the quality-of-life unlike SF36, as it
represents a single subjective dimension. Irene Moor et al. J Epidemiol Community Health. 2017
Jun.
the IBS self-diagnosis criteria are not exhaustive of the Rome IV criteria because it does not
consider the chronicity of the disorder. Priya Oka et al. Lancet Gastroenterol Hepatol. 2020 Oct.
Selection bias in the control population for self-rated health: absence of questions on cancer
history and surgical history.
The self-assessed mental health indicator (m-SRH) encompasses stress, depression and other
forms of mental problems whose genetics in some cases are known and in others are not.
Therefore, the suggestion that it may be linked to shared genes (MZ 0.23 vs DZ 0.04) is
not univocal because the data can be linked to genetic factors as well as to shared cognitive-
behavioral factors.
Review for 10.1186/s12876-022-02340-8 (2022)

Title: The relationships between IBS and perceptions of physical and mental health – a
Norwegian twin study
Version: 1 Date: 24 Apr 2022
Reviewer's report:
The relations between IBS and perceptions of physical and mental health - a twin Norwegian
study, addresses an interesting topic but presents important limitations.
The study carried out in 2014-2015 by means of a questionnaire sent by mail, should mention
the criteria of Rome III still valid in that period and not those of Rome IV published in
2016( limitation page19).
As reported by the authors themselves, the diagnosis of IBS was predominantly self-reported
and therefore unreliable as the exclusion of warning symptoms or concomitant somatic diseases.
Another important limitation is the lack of an adequate sample size.
Finally, the authors did not explain the reason for the exclusion of a population group between
20-40 years that could have had more IBS patients.
Best regards
Marco Soncini MD
Review for 10.1186/s12876-022-02342-6 (2022)

Title: Increased prescriptions for irritable bowel syndrome after the 2018 Japan Floods: a
longitudinal analysis based on the Japanese National Database of Health Insurance Claims and
Specific Health Checkups
Version: 0 Date: 30 Mar 2022
Reviewer:  Renato Bocchini
Reviewer's report:
the study is well written, well organized
Review for 10.1186/s12876-022-02311-z (2022)

Title: Nanomolar EP4 receptor potency and expression of eicosanoid-related enzymes in normal
appearing colonic mucosa from patients with colorectal neoplasia
Version: 1 Date: 09 Nov 2021
Reviewer's report:
Feddersen et al. present interesting data concerning the effects of PGE2 stimulation of colon
mucosa in both control and cancer patients. Furthermore they investigate expression of specific
enzymes and receptors and show differences in some and especially the LOX-pathway.  While
the results are interesting, there are some concerns.
Minor comments
1. For data showing patient data (such as EP-receptor expression) it would be helpful to show
single datapoints instead of bar graphs.
2. Was normality tested for patient data? Some error bars show very high variance and might
indicate non-normal distribution, necessitating other testing strategies. Again, this cannot be
evaluated in the absence of single datapoints.
Major comments
1. Fig. 2: The authors should also show ssc measurements for the other agonists. Similarly,
the proposed fits/ raw values for EP1 and EP3 should be shown. Additionally, although it is
mentioned in the text, the EP2 data are missing.
2. The fact that most antagonists did not prevent EP-receptor activation at all is alarming. It is not
clear to this reviewer how this could be explained. Subtype specific antagonists have been shown
to inhibit receptor signaling in a wide variety of in vivo/ex vivo and in vitro models.  For the
central claim that effects are EP4-receptor mediated, a different antagonist (i.e. ONO-AE3 208)
should also be used, especially as GW-x shows almost equipotent actions on the TP-receptor.
3. It is unclear how the novel data relate to the 2019 publication by the same authors.  Of note,
they find opposing results for EP1, Ep2, and EP3 receptors (the first two being not different  in
the first study, and EP3 being not significantly different in this study). While there might be an
explanation it is certainly no indication that there are “expressional alterations in at least 3 out
of 4 EP receptor subtypes present in normal appearing colonic mucosa from CRN patients”. As
the first study had higher n-numbers, it seems to be more reliable, but further data are needed.
4. Fig 3. Contains some data that only stem from one patient and other experiments have not
been performed at all/did not work. It is hard to justify the inclusion of this data in the study
as it is impossible to interpret.
5. A previous study found no effect of either ep1 or ep3 agonism on colonic mucosa but showed
effects of ep4 and ep2 agonism (•  DOI: 10.1016/j.ejphar.2012.06.020 ). How do the authors
explain the differences? Furthermore, did the authors test the non-selective EP1-3 antagonist
AH6809?
6. It is unclear to this reviewer what receptor high and receptor low means (e.g. Fig.3, Fig.4).
From the given information it seems like that are different methods for modelisation, but this
does not explain why n-numbers are different. It would be helpful to explain this in more detail.
7. To corroborate the differences in LOX-expression, IHC or WB should be performed.
Review for 10.1186/s12876-022-02311-z (2022)

Title: Nanomolar EP4 receptor potency and expression of eicosanoid-related enzymes in normal
appearing colonic mucosa from patients with colorectal neoplasia
Version: 3 Date: 18 Jan 2022
Reviewer:  #ukasz Zadka
Reviewer's report:
In my opinion, WB or IF methods could be performed even on a few samples, just to confirm the
presence of examined markers. Nevertheless, I accept the corrections introduced by the authors
and current version of the manuscript.
Review for 10.1186/s12876-022-02311-z (2022)

Title: Nanomolar EP4 receptor potency and expression of eicosanoid-related enzymes in normal
appearing colonic mucosa from patients with colorectal neoplasia
Version: 3 Date: 15 Feb 2022
Reviewer's report:
Review of “Nanomolar EP4 receptor potency and expression of eicosanoid-       related enzymes
in normal appearing colonic mucosa from patients with colorectal neoplasia” by Feddersen et al.
In this manuscript, the authors showed that biopsy samples from CRN react to prostaglandins
receptor agonists. In addition, mRNA expression of prostaglandin receptors and their related
gene was high in samples from CRN. This manuscript was already reviewed by another two
experts before this. And, authors well responded to comments from initial reviewers. However,
the data in this manuscript are too preliminary and not explored in sufficient detail to support
any clear conclusion. Some thoughts follow.
1. The major weakness of this study is that information of cell type in biopsy such as protein
expression or immune cell infiltration is missing. These differences may refer to these results.
Thus, it is hard to know the direct relationship between EP4 signaling and the pathogenesis of
CRN.
2. The information of inflammatory response in these biopsies is also missing. As the
authors described in the introduction, inflammation is the risk factor of CRC, information on
inflammation such as cytokine expression in biopsy is important to support the hypothesis of
this study.
3. How EC50 and SCC data were normalized? Protein levels or DNA contents in samples?
4. Ethnic information is missing
Review for 10.1186/s12876-022-02311-z (2022)

Title: Nanomolar EP4 receptor potency and expression of eicosanoid-related enzymes in normal
appearing colonic mucosa from patients with colorectal neoplasia
Version: 4 Date: 19 Apr 2022
Reviewer's report:
The authors answered well to my comments.
I understood that this study contains some difficulties and the authors strive to develop this
research field. I  expect for future studies.
I have nothing for further questions for publication.
Review for 10.1186/s12876-022-02311-z (2022)

Title: Nanomolar EP4 receptor potency and expression of eicosanoid-related enzymes in normal
appearing colonic mucosa from patients with colorectal neoplasia
Version: 4 Date: 25 Apr 2022
Reviewer:  #ukasz Zadka
Reviewer's report:
The authors entered the required amendments. I am fine with the current version of the
manuscript
Review for 10.1186/s12876-022-02299-6 (2022)

Title:  Immunohistochemical identification and assessment of the location of leptin, visfatin and
chemerin in the liver of men with different body mass index
Version: 1 Date: 31 May 2021
Reviewer's report:
Discussion section: in the fast decade, many study groups published different scientific articles
on this "hot" topic (i.e. PMID: 29557414, 29589386, 25561778). I suggest the Author to revise
the conclusion section, to underline the role of any single peptide studied, in the onset and
develpment of NAFLD, with regards to possible clinical application
Review for 10.1186/s12876-022-02299-6 (2022)

Title:  Immunohistochemical identification and assessment of the location of leptin, visfatin and
chemerin in the liver of men with different body mass index
Version: 1 Date: 21 Jun 2021
Reviewer's report:
The authors present a small study that evaluated the immunohistochemistry and mRNA
expression of 3 adipokines (leptin, visfatin and chemerin) in the liver of 14 liver organ-donors.
The study is interesting and original, but it should either be presented as a short communication/
letter or it needs further developments:
1) Was the number of patients necessary calculated or was this a convenience sample?
2) The immunohistochemistry/mRNA expression data should be controlled/correlated with
different variables: age, abdominal circumference, liver enzymes, serum levels of the studied
adipokines, adipose tissue expression, glucose levels/insulin resistance, serum lipid profile,
quantification of liver steatosis, inflammation or fibrosis.
Furthermore, I have real concerns regarding the immunohistochemistry of leptin. It may simply
reflect unspecific staining.
How do you explain the different results in immunohistochemistry and mRNA expression of
chemerin?
Review for 10.1186/s12876-022-02299-6 (2022)

Title:  Immunohistochemical identification and assessment of the location of leptin, visfatin and
chemerin in the liver of men with different body mass index
Version: 2 Date: 03 Oct 2021
Reviewer's report:
Even though it is an interesting topic, the authors present a very pilot study with a small number
of cases (and N was not predefined), without relevant information regarding confounders. I
have suggested the authors to present it as a short communication. The authors agreed but did
not reformulate the manuscript as a short communication. It is still presented as a full-research
article.
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 1 Date: 30 Mar 2022
Reviewer:  Masaji Hashimoto
Reviewer's report:
The conclusion of this study was FAR had higher predictive accuracy than other inflammation-
based models and AFP.  The reason of this superiority comparing other inflammation-based
models was leukocyte-based markers were often affected by other factors and might not reflect
the inflammatory state of cancer patients. How  and when the results of NAR, PLR, MLR and
SII in Table 2 and Table 3 were calculated? Were the results in each patients calculated in one
point or the mean value of several point?
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 1 Date: 30 Mar 2022
Reviewer's report:
Except that Wu et al. reported prognostic value of FAR in predicting the prognosis of HCC
after hepatectomy, there's no other relevant studies concentrated on FRA and hepatectomy.
The authors compared the efficiency of FAR and other indicators of inflammatory factors and
AFP in predicting patients' outcomes after hepatectomy. This contributes to the accumulation
of evidence. However, limitations
major:
1.The authors mainly illustrated that FAR performed better than the other indexes by the
conclusions in Figure 1 and supplementary table 1, but in both tables, the t-roc was similar before
20 months/2 years, and the difference in FAR was obvious 20 months after hepatectomy, and
the t-roc of FAR was constantly increasing, especially in Figure 2b, where the t-roc curve of
FAR was almost constantly increasing, how can the authors explain this reason; Furthermore,
based on such results, is it possible to state that FAR outperforms other metrics?
2.Since four digit patients are included, why not design a training cohort and a validation cohort?
minor#
1.Ref 1 needs to be updated
2.Table 1 is missing a footnote; for eg: Age was presented as mean?/median? In the results
section, the authors stated a mean age of 50, and in the statistic analysis, the authors stated
Continuous variables are shown as medians
3.It is necessary to explain whether the operation is accomplished open or through laparoscopy
4.Subsequent treatment after progression included radiofrequency, chemotherapy, re-operation
or targeted therapy as appropriate. Does this have an impact on the OS of patients
5.Both fibrinogen and albumin are dynamically changing, can the authors present the time of
detection of this indicator?
6.table 1, Why not present the relevant content of Child-Pugh and AST
7.table 2 and 3, Categorical variables should be presented in a certain classification, like 'Child-
Puugh grade B' instead of 'Child-Pugh grade'; 'BCLC stage C?' instead of 'BCLC stage' only
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 1 Date: 04 Apr 2022
Reviewer:  Katsunori Imai
Reviewer's report:
The manuscript entitled ‘Preoperative fibrinogen-to-albumin ratio predicts the prognosis of
patients with hepatocellular carcinoma subjected to hepatectomy’ by Rong-yun Mai et al.
reported the prognostic value of FAR in patients with HCC who underwent hepatectomy.
The manuscript is well written and the results shown in this study are informative.
Some points are listed for the authors’ consideration.
Comments
1. In the discussion section, similar things are written with the introduction section. The authors
should avoid to repeat to write similar things in the introduction and discussion sections.
2. Why were the blood transfusion and the extent of resection related to FAR?
3. The prognosis of HCC is usually influenced by two factors, including tumor factors and
background liver function factors. The authors should clarify the reason and mechanism why
FAR is associated with long-term outcomes in patients with HCC.
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 1 Date: 12 Apr 2022
Reviewer:  Taku Aoki
Reviewer's report:
In the present manuscript, Mai et al. examined the impact of fibrinogen-to-albumin (FAR) on
patient outcomes with hepatocellular carcinoma (HCC) undergoing surgery. They concluded
that this parameter was useful for predicting prognoses of patients with HCC, and its impact
was greater than that of alpha-fetoprotein.
1. What is the clinical relevance of this factor? If the value is high, do the authors abandon
the operation? Numerous papers have evaluated the significance of inflammation/nutrition-
associated parameters in patients with HCC, and this paper dealt with another novel index.
However, none of them has been introduced into the daily practice of HCC.
2. The authors estimated the value of FAR in the same cohort. The authors are requested to
validate the significance of FAR in another validation cohort.
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 2 Date: 07 May 2022
Reviewer:  Taku Aoki
Reviewer's report:
In the revised manuscript, the authors have responded appropriately to the questions raised by
the rviewers. Now, I have no additional comments.
Review for 10.1186/s12876-022-02328-4 (2022)

Title: Preoperative fibrinogen-to-albumin ratio predicts the prognosis of patients with
hepatocellular carcinoma subjected to hepatectomy
Version: 2 Date: 08 May 2022
Reviewer:  Masaji Hashimoto
Reviewer's report:
The comments from  the reviewers have been addresses and fixed.
Review for 10.1186/s12876-022-02331-9 (2022)

Title: Colorectal Cancer Screening Participation among Citizens not recommended to be
screened: A Cohort Study
Version: 1 Date: 16 Feb 2022
Reviewer:  Isabel Portillo
Reviewer's report:
Dear authors,
Thank you very much for your paper. However, I would like you answer some questions?
- Because of you unknowing the appropriate surveillance in all high risk people (including all
cases of not average risk of CRC), your results and conclusions are not very accurate . In fact,
there are published papers that show difficulties and missed surveillance in those patients.
- Methods could be improved if you have all database (gender,  age group, deprivation,
comorbidities are important ítems to take into account)
- The threshold of FIT is not adjusted by  mcg Hb/g feces (standard). If you mean 100ng /ml
buffer, you should convert in 20mcg/g feces for OC-Sensor.
- Some cases of  IBD and high risk are diagnosed because of their participation. Positive cases
and colonoscopy. Therefore,  false positive rate could be lower than your hipothesis
Review for 10.1186/s12876-022-02331-9 (2022)

Title: Colorectal Cancer Screening Participation among Citizens not recommended to be
screened: A Cohort Study
Version: 2 Date: 25 Mar 2022
Reviewer's report:
The manuscript has improved significantly and is now much more clear and straightforward. I
have spotted two minor errors:
line 95 (document without tracking changes): Exempt from this WAS residents --> should be
"WERE"
line 255 : the word "despite" is redundant
Otherwise I have no further comments. I appreciate and recognize authors' effort to review the
manuscript, incorporate and answer to all the reviewers' comments.
Review for 10.1186/s12876-022-02331-9 (2022)

Title: Colorectal Cancer Screening Participation among Citizens not recommended to be
screened: A Cohort Study
Version: 2 Date: 05 May 2022
Reviewer:  Isabel Portillo
Reviewer's report:
Dear authors,
I am deligthed to Review your paper. I suggest to follow-up this issue and include more cases
in order to give some highlight for programmes and authours
Best Regards
Review for 10.1186/s12876-022-02335-5 (2022)

Title: Optical biopsy for esophageal squamous cell neoplasia by using endocytoscopy
Version: 3 Date: 09 Mar 2022
Reviewer's report:
Comments to the Author
In this article, the authors reported a prospective study to assess the performance of
endocytoscopy for optical biopsy of esophageal squamous cancer. Among 197 high-risk
subjects, 90 patients were detected to have suspected esophageal lesions after WLI and NBI,
37 of them (41 lesions) were characterized as esophageal SCC by endocytoscopy. They found
endocytoscopy has a high diagnostic accuracy (98.9%) and there were no false positives in
cases of SCC. They concluded that optical biopsy by using ECS for esophageal lesions that are
suspected to be tumorous is sufficient in clinical practice. The topic is interesting, but I have
the following comments.
Major and specific comments:
1. The definition of SCC, and high-grade intraepithelial neoplasia (HGIN), low-grade IN,
should be clarified. Also, how to classify the HGIN based on the EC classification?  Could all
intraepithelial neoplasia (HGIN, LGIN) be followed up alone without resection?
2. According to the flow-chart of patients’ enrollment, 90 patients were detected to have
suspected tumor in esophagus by WLI and NBI. However, finally only 37 patients (41 lesions)
have confirmed SCC. The diagnostic accuracy of NBI seems to be very poor (<50%) and is not
consisted with previous reports. The author should clarify this point.
3. In method section, the author mentioned “ESD was later performed for lesions that were
diagnosed to be esophageal SCC by ECS”. However, in the result section, one patient was
diagnosed EC3 lesion (cancer) received biopsy not ESD. These data are not consistent.
4. Did the patients receive NBI with conventional magnification or ultra-high magnification
(endocytoscope) to observe the IPCL pattern and to predict the histology? If it is true, these
should be described.
5. Because all patients had received WLI, NBI and endocyto, the additional benefit of endocyto
on other modality should be analyzed. Currently, we have so many image-enhanced modalities
for diagnosis of ESCC, the author should emphasize the advantages of endocyto and convince
the readers about the benefit of a new modality. Especially, conventional magnifying endoscopy
is now a commonly used and easily operated tool for diagnosis of ESCC with a high accuracy
in daily practice. The procedure time may be longer, and the operation skills or interpretation
may be more complicated by endocytoscopy. These potential disadvantages of endocyto should
be discussed in the discussion section.
6. It’s difficult to differentiate the EC3 in figure 3 from the EC2 in figure 4. The cellular structures
under endocytoscopy seemed to be preserved in figure 3, and it may be classified as EC2. The
authors should demonstrate more clearly the features of EC classification.
Review for 10.1186/s12876-022-02335-5 (2022)

Title: Optical biopsy for esophageal squamous cell neoplasia by using endocytoscopy
Version: 5 Date: 03 May 2022
Reviewer:  Akira Yokoyama
Reviewer's report:
Major comment
This paper shows that Endocytoscopy can differentiate dysplasia from cancer with extremely
high accuracy. The classification is clear in typical cases, but there are always borderline cases.
As Reviewer 2 pointed out, EC2 and EC3 are similar in typical cases, and the EC classification
cannot be validated correctly unless it is performed by a large number of endoscopists at other
institutions. Although this is a prospective, prospective study, it was conducted at only two
institutions, and although the number of endoscopists was not stated, it was probably conducted
by a small number of endoscopists, which does not make sense for a multicenter prospective
study as it should. We consider this to be a fatal problem in drawing conclusions for this paper.
On the other hand, as the results analyzed in this study design, we do not see any particular
problem with the analysis method, etc.
Minor comment
Endoscopist information should be included in the METHODS of the paper
Review for 10.1186/s12876-022-02333-7 (2022)

Title: Biliary obstruction and pancreatitis after duodenal stent placement in the descending
duodenum: a retrospective study
Version: 2 Date: 24 Mar 2022
Reviewer's report:
This is a clinically interesting study investigating duodenal stent-related risk factors for
cholangitis and/or pancreatitis. However, there are several issues in this paper that need to be
reconsidered.
1. The authors considered that the risk factors for cholangitis/pancreatitis obtained from this
study might mainly result in the orifice obstruction of duodenal major papilla, which may
increase intraductal pressure of biliary tract and/or pancreatic ducts.
A) In pancreatitis, I agree with the mechanism. However, it is questionable whether a similar
mechanism could be the cause in cholangitis. The diagnosis of cholangitis was described as
"fever lasting >24 hours with cholestasis”. There was no description whether biliary infection
was presented or not, so the details are not available. Although presumably aseptic cholangitis
was not common in this cohort, the fever was caused by infection combined with cholestasis.
Increased intraductal pressure of biliary tract may cause cholestasis, resulting in pain and/or
jaundice, but not always accompanied by fever. Thus, the question arises against combining
cholangitis and pancreatitis together and considering risk factors.
B) There are also significant clinical differences between cholangitis and pancreatitis, including
drainage methods and outcomes in severe cases. It was mentioned as limitation of this study that
there was a problem with the number of cases, but it seems that there is not much difference
between 11 cases of cholangitis and/or pancreatitis and 9 cases of cholangitis. It would be of
more clinical value to examine risk factors for each group, separately.
C) When considering cholangitis, it would be more meaningful if not only risk factors for
cholestasis but also for biliary infection (e.g., inflammatory findings prior to duodenal stent
placement) could be taken into account.
2. Were all cases of pancreatitis cancers other than pancreatic cancer? Pancreatic cancer located
in groove lesion or uncinate process are not always accompanied by obstruction of the MPD,
and how is the evaluation of dilated MPD handled in pancreatic cancer cases?
#.  In which primary diseases was tumor invasion to the major duodenal papilla most frequently
observed?
Review for 10.1186/s12876-022-02333-7 (2022)

Title: Biliary obstruction and pancreatitis after duodenal stent placement in the descending
duodenum: a retrospective study
Version: 2 Date: 28 Mar 2022
Reviewer's report:
This is a review of manuscript No. 4d85c09a-908f-4685-a20a-2466ae269578, entitled " Acute
cholangitis and pancreatitis after duodenal stent placement in the descending duodenum: a
retrospective study" Though it is interesting, there are still many points that need to be revised.
Major Comments:
Conditions that cause stenosis in the descending duodenum are often complicated by bile
duct stricture. This is a condition that requires conquering two problems. Although this is an
important issue to consider, there is insufficient information and the content does not provide
a vision of actual clinical practice.
Cholangitis often requires drainage, while pancreatitis is treated conservatively. Considering
these two different invasive diseases together may obscure the issue. In fact, this manuscript
provides a solid discussion of bile duct drainage before and after DSP, but the inclusion of cases
of pancreatitis in the statistics diminishes the significance of the results of the study.
We suggest a little more focus on duodenal stenting and cholangitis.
Minor comments
1) Page3, line51
Throughout the manuscript, only “SEMS” is used for both biliary and duodenal, making it
difficult to understand the meaning of the text at times.
2) Page5, line80
Both Covered and Uncovered duodenal stents have been incorporated into the study. These two
types of stents have sometimes been subjected to comparative studies. The number of cases in
which Covered SEMS was actually used was small. It is suggested that Covered SEMS cases
be excluded from this study.
3) Page6, line103
Although the report mentions the presence of a bile duct stent, the bile duct stent is a device for
which TRBO after implantation is discussed. If cholangitis triggered by DSP is to be discussed,
a bile duct stent that was originally nearly obstructed should be excluded, and at least the period
of time that has elapsed since implantation should be noted. Since the onset of cholangitis leads
to withdrawal of chemotherapy, the bile duct stent may undergo periodic replacement.
4) Page8, line136
How about charting the Study enrolment.
5) Page8, line141
Any abnormal values in biliary enzymes prior to DSP should be noted.
6) Page10, line176
It should state "First,...,before DSP."
7) Page10, line180
This study evaluates short-term AEs. What is the long-term prognosis for patients with DSP
only, without prophylactic bile duct stenting?
8) Page11, line191
It is unclear why the creation of space would lead to pressure on the main papilla. A more
detailed description is requested.
Review for 10.1186/s12876-022-02333-7 (2022)

Title: Biliary obstruction and pancreatitis after duodenal stent placement in the descending
duodenum: a retrospective study
Version: 2 Date: 02 Apr 2022
Reviewer's report:
The authors retrospectively evaluated the risk factors for acute cholangitis and/or pancreatitis
after duodenal stent placement in the descending duodenum. The multivariate analysis indicated
that female sex, absence of biliary stents, and tumor invasion to the major duodenal papilla
were significant independent risk factors for acute cholangitis and/or pancreatitis. This study is
useful for the readers who manage malignant gastric outlet obstruction (GOO). I have several
comments for the authors.
Major
1. Sixty-five patients who underwent duodenal SEMS placement in the descending duodenum
were enrolled in this study. Were major duodenal papilla covered with duodenal SEMS in all
65 patients?
2. Thirty-four patients underwent biliary stent placement in this study. What were the intervals
between biliary stent placement and duodenal SEMS placement? Were there any patients who
underwent both biliary stent and duodenal SEMS placement on the same day? The incidences
of pancreatitis might be affected by the placement of biliary stent placement on the same day.
3. What is the length of biliary SEMS in the duodenal portion (distal side of biliary SEMS in
the D2) in the authors’ institution?
4. How did the authors treat the patients with both biliary obstruction and GOO in this study?
Which one of these 4 methods is these patients applicable to?
A) Biliary stent to Duodenal SEMS on separate days
B) Biliary stent to Duodenal SEMS on the same day
C) Duodenal SEMS to EUS-BD on separate days
D) Duodenal SEMS to EUS-BD on the same day
5. Eleven cholangitis after duodenal SEMS placement was observed in this study. Three patients
were treated with antibiotic therapy alone, and six underwent biliary drainage along with
antibiotic administration. How did the authors select conservative or interventional therapy?
Could PTBD tube be removed after the improvement of cholangitis in three PTBD cases?
6. The number of events (acute cholangitis and/or pancreatitis) is eleven. The authors evaluated
4 variables in multivariate analysis. The number of events might be insufficient for multivariate
analysis.
Minor
1. Did the authors obtain histological evidence in all 65 patients?
Review for 10.1186/s12876-022-02333-7 (2022)

Title: Biliary obstruction and pancreatitis after duodenal stent placement in the descending
duodenum: a retrospective study
Version: 2 Date: 11 Apr 2022
Reviewer:  Wenjian Mao
Reviewer's report:
This manuscript reports the results of a retrospective study to identify some risk factors for acute
cholangitis and/or pancreatitis after duodenal stent placement in the descending duodenum and
found that female sex, absence of biliary stents, and tumor invasion to the major duodenal papilla
are the primary risk factors.
The authors are to be complimented on what appears to be a well-designed study of an important
question.  These findings can allow endoscopists to better identify patients at significant risk
and potentially affect clinical decision-making, but still need further validation.
I list my major concerns as below:
Firstly, the definition of acute pancreatitis is not entirely appropriate in the method section.
The diagnosis of acute pancreatitis is defined as meeting at least two of the three following
criteria: (1) abdominal pain consistent with acute pancreatitis; (2) serum lipase (or amylase)
activity greater than three times the upper limit of normal; (3) characteristic findings of acute
pancreatitis on contrast-enhanced computed tomography (CECT) or less commonly magnetic
resonance imaging (MRI) or transabdominal ultrasonography according to the revision of the
Atlanta classification (RAC) criteria.
Secondly, what's the reason for dividing age into > 69 and #69.
Thirdly, as reported by the authors, it is a single center retrospective study including a low
number of patients and thus the individual risk for cholangitis and pancreatitis could not be
evaluated. The results of this study need to be carefully interpreted and further explored.
Review for 10.1186/s12876-022-02333-7 (2022)

Title: Biliary obstruction and pancreatitis after duodenal stent placement in the descending
duodenum: a retrospective study
Version: 2 Date: 18 Apr 2022
Reviewer's report:
The authors describe risk factors when stent placement in the descending duodenum causes acute
cholangitis and pancreatitis.
It is very important to assess the risk of treatment when performing endoscopic treatment.
But the following points require further elaboration.
Major points
What is the significance of performing a risk assessment that combines cholangitis and
pancreatitis?
In this report as well, the treatments for cholangitis and pancreatitis are different, and I would
like to know the risks of each.
Minor points
P3, L56: Reference [12] is about stent placement for distal bile duct stenosis and dose not
describe duodenal stents, please delete it.
P5, L86-89: The explanations in Figures 1a and 1b are different from the actual figures. Please
write the appropriate text.
P6, L101-103: Did the author measure the diameter with CT images? Please describe so that
you can see which modality you used.
P8, L150-151: Please consider in the discussion that there is a significant difference in the
duration of onset of pancreatitis and cholangitis.
Fig 1a: Please insert a mark on the figure to identify the location of the stenosis.
Table 2: If you have made a statistical evaluation, please describe the result.
Review for 10.1186/s12876-022-02334-6 (2022)

Title: Intestinal fatty acid binding protein is a disease biomarker in paediatric coeliac disease
and Crohn’s disease
Version: 2 Date: 29 Jun 2021
Reviewer's report:
Thank you for the opportunity to review.  This is an important area oto be examining in the
IBD/ coeliac disease literature.  Unfortunately, there are a number of problems with the paper
as outlined below.
It is noted that this study was completed 8 years ago making it difficult for the authors to address
some of the issues.
The aims/hypothesis(es) are not clear - is the aim to establish whether iFABP are an alternative
to other measures for IBD assessment. And replace antibodies?Regarding the study flow (Figure
1) - it is not clear why there was loss to follow up for some participants and why some samples
are missing.
Throughout the paper - convention to have 'Coeliac' with lower case 'c' and to use 'coeliac disease'
or 'patients with coeliac disease'
Regarding 'patient characteristics' it would be helpful to have a brief summary of the breakdown
of patients - coeliac, controls, IBD
The absence of histological correlates is a major weakness of the study - although patients
seemed compliant, what evidence is there that the mucosa healed?
Table 1 represents a univariate analysis - was there any attempt at mutlivariate analysis? is there
a need to adjust with Bonferroni correction? Statistical opinion might be helpful.  A statistical
opinion might also inform an analysis of the performance of the iFABP compared to available
tests.
The lines and asterixes in the figures are confusing to the eye and not consistent with convention
- these could be revised.
The groups are also confusing - there appear to be 3 groups with coeliac disease - newly
diagnosed, 6 months and 12 months.  Is ‘established’ 6 months or 12 months? This makes the
results section confusing to the reader in cross referencing tables and figures.
Discussion: Whilst there were changes in some biomarkers with treatment, it is not clear whether
this is because of treatment success or other factors (as mentioned earlier regarding histology).
I don't think we can conclude that iFABP helps with diagnosis based on these results.