JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-12-175 (2012)

Reviewer's report
Title:Dyspeptic Symptoms and Delayed Gastric Emptying of Solids in Patients
with Inactive Crohn's Disease.
Version: 1Date:2 April 2012
Reviewer: J Keller
Reviewer's report:
Reviewer's report
-----------------
The authors investigated 26 patients with inactive Crohn’s disease as indicated
by CDAI < 150. They performed 13C-octanoic breath tests for measurement of
gastric emptying of solids and used a questionnaire for evaluation of dyspeptic
symptoms. Their data confirm that a subset of patients with CD, who have no
clinical evidence of inflammatory activity, show delayed gastric emptying. They
also show an association between delayed gastric emptying and dyspeptic
symptoms which has not been assessed before in CD patients. Thus, their
findings may be of pathophysiological relevance. However, some methodological
aspects need clarification and interpretation of some of the results remains
unclear.
Major compulsory revisions:
1. The symptom questionnaire used is not well known and, thus, the authors
should describe it in more detail (e.g. how does a questionnaire asking for 5
items result in a maximum of 44? what does a score of 6 mean?)
2. The authors claim to have used the methodolgy established by Ghoos et al.
and to have taken normal data derived from this study into account. However, the
upper limit of normal was well below 200 min in the study published by Ghoos et
al. Moreover, 15-20% of the control subjects have pathologically delayed gastric
emptying or at least borderline results according to the normal values given (fig.
1). These aspects need further explanation.
3. Intra- and interindividual variability of gastric emptying is rather high. In
contrast, the authors report extremely small standard deviations (?) for t lag and t
1/2. Please explain.
4. Data for t ½ in CD patients with and without dyspepsia are largely overlapping
(fig 2). Please state statistic test used and the exact p-value when comparing
these data.
5. The mean PADYQ score for vomiting in CD patients is extremely low (fig. 3: <1
in pts with normal gastric emptying, <2 in patients with delayed GE) and standard
deviation (?) is small. How is it possible that the authors observed a significant
correlation between gastric emptying velocity and PADYQ score fort his specific
subscale?
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-175 (2012)

Reviewer's report
Title:Dyspeptic Symptoms and Delayed Gastric Emptying of Solids in Patients
with Inactive Crohn's Disease.
Version: 1Date:1 July 2012
Reviewer: Halina Cichoz-Lach
Reviewer's report:
The paper concerns the issue of dyspeptic symptoms and delayed gastric
empting of solids in patients with inactive Crohn disease. The problem is very
interesting. The Authors concluded that delayed gastric empting is associated
with dyspeptic symptoms, particularly vomiting even without any evidence of
gastrointestinal obstruction.
I have several comments among which the following is the most essential which
required major revision:
1. The population examined is relatively small. I realized that this paper is one of
a few in this issue but in my opinion 26 subjects is too poor population to obtain
strong conclusions.
2. The Discussion is too long with unnecessary. I strongly suggest to shorten it in
order to obtain better clarity of message.
The remaining comments which required minor revision:
3. No information is provided about treatment of Crohn disease in examined
patients (e.i. steroids?).
4. In the section Study subjects statement of …”Subjects aged <18 years old, or
presenting…” (page 4) should be removed, because this information was placed
in the onset of section (26-67 ranging years old).
5. Clinical characteristics of the study subjects should be summarized in a table
instead of text. This will improve readibility of the presentation.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-12-175 (2012)

Reviewer's report
Title:Dyspeptic Symptoms and Delayed Gastric Emptying of Solids in Patients
with Inactive Crohn's Disease.
Version: 2Date:4 September 2012
Reviewer: Halina Cichoz-Lach
Reviewer's report:
I read the revised manuscript and answers to reviewers. I accept all corrections.
Review for 10.1186/1471-230X-12-175 (2012)

Reviewer's report
Title:Dyspeptic Symptoms and Delayed Gastric Emptying of Solids in Patients
with Inactive Crohn's Disease.
Version: 2Date:14 September 2012
Reviewer: J Keller
Reviewer's report:
Comment 2: The authors’ response does not answer my question. The upper
limit of normal for t ½ given by Ghoos et al. (Gastroenterology 1993) is 118 min.
Why did the authors choose 200 min and how do they explain that 3 out of 14
healthy subjects have delayed gastric emptying even when considering values
up to 200 min as normal? According to a previous analysis in more than 1000
patients age has no influence on t 1/2 when using the Ghoos method (Keller et
al. Neurogastroenterol Motil 2009).
Comment 5: From the data given in the manuscript I still doubt that there can be
a significant association between PADYQ score for vomiting and gastric
emptying velocity. It would be helpful to see the correlation.
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-12-175 (2012)

Reviewer's report
Title:Dyspeptic Symptoms and Delayed Gastric Emptying of Solids in Patients
with Inactive Crohn's Disease.
Version: 3Date:14 November 2012
Reviewer: J Keller
Reviewer's report:
My concerns have been addressed.
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-12-174 (2012)

Reviewer's report
Title:Systemic lupus erythematosus complicated by Crohn's disease: a case
report and literature review
Version: 2Date:24 July 2012
Reviewer: Farida Al Balushi
Reviewer's report:
The association between SLE and crohns disease is well known but rare , there
are few case reports that already addressed this association ( around 6 cases in
English literature but few more in other languages ) in addition to that there is a
recently published systematic review which covered this association , please
check the following ( Inflammatory bowel disease and lupus: A systematic review
of the literature Review Article
Journal of Crohn's and Colitis, Volume 6, Issue 7, August 2012, Pages 735-742
Konstantinos H. Katsanos, Paraskevi V. Voulgari, Epameinondas V. Tsianos )
This case report is not particularly unique except for the long duration between
the diagnosis of SLE and onset of crohns disease, however accumulation of case
reports of such a rare association could be of value in clinical practice and future
research studies.
There are no major compulsory or minor essential revisions .
Discretionary revision ;
1- It would be useful if the authors provide us with the Radiological findings in the
present case like abdominal CT scan that would highlight potential discriminatory
findings between SLE and Crohns before histopathology results become
available.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-174 (2012)

Reviewer's report
Title:Systemic lupus erythematosus complicated by Crohn's disease: a case
report and literature review
Version: 2Date:5 October 2012
Reviewer: Gottfried Novacek
Reviewer's report:
This is an interesting report of a patient with systemic lupus erythematosus (SLE)
and crohn colitis. She suffered from gastrointestinal bleeding and diarrhea.
Findings at colonoscpy as well as histopathological changes led to the diagnosis
of Crohn's disease. The patient responded well to infliximab.
Major Compulsory Revision
1) Case presentation/last paragraph: The authors should describe the dosage of
infliximab and the intervals between the infusions, the observation period after
the start of infliximab, if their was a loss of response, and more objective
parameters for treatment response such as CRP and HBI or CDAI.
Discretionary Revisions
1) Case presentation/1st paragraph: In which parts of colon were the ulcers
located? Was the terminal ileum investigated and what was it look like? This
questions should be answered for all mentioned colonoscopies.
2) Case presentation/1st paragraph: The patient received prednisolone for a very
long time. Why was cyclophosphamide never given to the patient?
3) Discussion/8. paragraph: I suggest to change the 2nd sentence: However,
longterm treatment with glucocorticosteroids should be avoided. In case of
steroid dependency or steroid refractory TNF-alpha blockers are an effective
treatment to induce and maintain remission.
4) Discussion: The authors should discuss the knowledge about the
effectiveness of infliximab for SLE and especially gastrointestinal symptoms
caused by SLE. The authors describe that TNF-alpha blockers can cause
drug-induced lupus, but can they also improve SLE?
5) References: The following reference should be included in the list: Katsanos
KH, et al. JCC 2012;6:735-42.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests' below.
Review for 10.1186/1471-230X-12-173 (2012)

Reviewer's report
Title:Percutaneous ultrasonographically guided liver punctures: A study of 2007
patients over 10 years
Version: 1Date:24 April 2012
Reviewer: Matthias J. Bahr
Reviewer's report:
- The study is presented as prospective. However, substantial proportions of the
data were gathered retrospectively (e.g. coagulation parameters.
- Introduction: Some points are clearly overstated. There is, for example, no
paucity of quantitative data on liver biopsy, though we still need more data.
- Introduction: Incorrect presentation of the context of references (e.g. ref. 2
represents an AASLD position paper not a clinical study).
- Relevant references were not cited (e.g. WEST J, CARD TR.
GASTROENTEROLOGY 2010; 139: 1230-1237 | SEEFF LB et al. CLIN
GASTROENTEROL HEPATOL 2010; 8: 877-883)
- Methods, nomenclature: Can be substantially shortened.
- Methods, patient selection: Data presentation should be focused on liver
biopsy.
- Results: Patient ages ranged from 3 months to 96 years. It appears
inappropriate to have small children in the study. These patients should be
analyzed separately.
- Figure 2: Data should be restricted to liver biopsies
- Figures: Data do not benefit from being shown as figures, tables replacing both
figures appear preferable
MINOR
- Thorough revision by a native speaker is recommended.
- Data presentation: significance values (i.e. p-values) should be given using one
valid digit (e.g. p = 0.01 instead of p = 0.0112)
- References should present original titles rather than translations (e.g. ref. 4)
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-173 (2012)

Reviewer's report
Title:Percutaneous ultrasonographically guided liver punctures: An analysis of
1961 patients over a period of ten years
Version: 2Date:10 July 2012
Reviewer: Holger Lutz
Reviewer's report:
- Major Compulsory Revisions
1. Though stated otherwise in the cover letter, the terms of liver “puncture” and
PP are still used in parts of the manuscript. Please apply the changes mentioned
in the cover letter to the whole manuscript.
2. The authors claim, that most of the biopsies are performed on an ambulatory
basis, while in the presented study, two thirds are performed in inpatients. Please
comment on that.
3. The authors still describe their study as “prospective”, though e.g. coagulation
parameters (which are essential for their analyses) were only obtained in 34 %of
all patients. How could biopsies be performed when coagulation parameters
appear to be missing in 66% of the patients? This issue has to be addressed and
data collection has to be changed to retrospective as the study design with
missing data and defined criteria does not fulfill the requirements of a prospective
study.
4. Abbreviations, if used, have to be explained or avoided if only used once (see
discussion, “BC” and “SB”).
5. Missing data on severity of liver disease (fibrosis grade) in patients with
complications compared to patients without is disappointing. In that case,
grouping of diseases in Table 1 for better understanding and smaller table size is
recommended. Furthermore, language should be English throughout the whole
manuscript (“Metastase eines Gastrointestinalen Tumors”). Please revise the
manuscript thoroughly.
- Minor Essential Revisions
1. Wikipedia links should be removed from the manuscript (see legends for
tables 2 and 3).
2. Tables 2 and 3 should be combined in one table.
3. It does not seem to provide any useful information if different types of
metastases are described in detail; this group should be summarized as
“metastases”.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-173 (2012)

Reviewer's report
Title:Percutaneous ultrasonographically guided liver punctures: An analysis of
1961 patients over a period of ten years
Version: 2Date:15 July 2012
Reviewer: Matthias J. Bahr
Reviewer's report:
The authors did address all relevant points of critique appropriately.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-172 (2012)

Reviewer's report
Title:Murine CD4+CD25- cells activated in vitro with PMA/ionomycin and
anti-CD3 acquire regulatory function and ameliorate experimental colitis in vivo
Version: 1Date:5 October 2012
Reviewer: Franco Scaldaferri
Reviewer's report:
Potentially interesting paper, assessing the T regulatory capacity of subset of T
cells manipulated in vitro in the experimental murine CD45RB transfer model of
colitis.
Well written, clear however it displays several major limitations.
Authors state that murine cd4+cd25- cells activated in vitro with pma/ionomycin
and anti-cd3 acquire regulatory function.
However, even if they are associated to a “clinical amelioration” of colitis in mice,
the causality could not be related so strictly to those “supposed” transferred
regulatory T cells.
Those cells, in fact, have not been fully characterized in vitro, in simplified
system. Do they display regulatory properties in vitro? are they able to suppress
proliferation of activated T cells in a dose dependent manner? Do they inhibit T
cells cytokines production upon activation?
Do they stay alive in mice following the transfer?
Furthermore, authors state that it is the treatment with pma/ionomycin, by
modulating ion channel function, that enhances the expression of cd25 on murine
cd4+cd25- cells. A control group of mice receiving cd4+cd25- cells activated only
with anti-CD3 and then cultured in IL2 supplemented medium should also be
included in the paper.
Finally introduction should contain more information about stimulation of T cells
with (PMA)/ionomycin and anti-CD3.
Aim of the study should be stated instead of anticipating, already in the
introduction, results of the study and analysis.
In the discussion session more room should be dedicated to compare
pma/ionomycin and anti-cd3-activated murine cd4+cd25- cells to other in vitro
generated regulatory T cells. Limits of the paper should also be better presented.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests'
Review for 10.1186/1471-230X-12-172 (2012)

Reviewer's report
Title:Murine CD4+CD25- cells activated in vitro with PMA/ionomycin and
anti-CD3 acquire regulatory function and ameliorate experimental colitis in vivo
Version: 1Date:18 October 2012
Reviewer: Marinos Kallikourdis
Reviewer's report:
In this manuscript Majowicz and coworkers elegantly show that CD4+CD25- T
cells activated in vitro via PMA/ionomycin express Treg-like markers and are able
to reduce the disease severity of experimental colitis.
The experimental methods are well-described and the experiments follow a
logical sequence and are thoroughly executed and reported. The in vivo
protective effect is studied from a variety of parameters and is convincing.
There is one issue with the interpretation of the results, which I outline below.
Discretionary Revisions:
The manuscript does not present data examining the in vitro suppressive
capacity of these cells. Whilst this could be considered not necessary, given the
convincing in vivo data, presenting in vitro suppression data could substantially
strengthen the conclusions drawn by the in vivo studies.
Minor Essential Revisions:
The number of CD45RBlow cells injected in “negative control” animals should be
stated.
Major Compulsory Revisions:
Experimental colitis, as performed by the authors and by many of the previous
reports cited, is induced by administration of 4*105 CD45RBhi T cells into a
lymphopenic recipient. Administration of an equal number of CD45RBLow cells
can protect from colitis, as indeed the authors and others have shown. However,
as shown in Barthlott, Kassiotis and Stockinger, J Exp Med (2003), injection of
increased numbers (6*106) of CD45RBhi cells, that have no suppressive
capacity, is sufficient to show a reduction in the severity of colitis, due to
“competition with neighboring T cells for limited resourses” that limits the
activation of the T cells in the lymphopenic host.
The authors used 1.2*106 TregPMA cells, which is appreciably less than the
number used by Barthlott and colleagues, though still 3 times more than the
number of CD45RBhi that cause the colitis. As a consequence, it is not possible
to exclude that at least part of the protective effect observed in vivo is not due to
the increased number of administered cells.
This caveat should be made clear in the discussion.
Dr M Kallikourdis
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-171 (2012)

Reviewer's report
Title:The Zelnorm Epidemiologic Study (ZEST): A Cohort Study Evaluating
Incidence of Abdominal and Pelvic Surgery related to Tegaserod Treatment
Version: 2Date:19 July 2012
Reviewer: Allen Brinker
Reviewer's report:
Major Compulsory Revisions
None
Minor Essential Revisions
None
Discretionary Revisions
Additional limitations needed - I believe the authors should offer further
discussion on the issue of misclassification afforded with selection of the
comparator arm of this and any observational study of IBS patients. As noted in
the literature (1,2), there appears to be substantial clinical heterogeneity of the
application of ICD codes within this population so as to make comparator cohorts
challenging. As noted by the authors in the Discussion and with interest in
patients with IBS, “gallbladder surgery may be used as part of a symptom
evaluation in some patients.” Unless an EMR / claims database can claim a
substantial portion of an adult’s life so as to capture gallbladder surgery in the
remote past, it may not be possible to derive a meaningful inference for incident
gall bladder surgery. Misclassification of this nature leads to the null – as was
reported for this study for gall badder surgery. Other outcomes – abdominal
surgeries in general – may not be differential and so may be better endpoints for
study other than gallbladder surgery.
1. Brinker A, Avigan M. Epidemiology of ischaemic colitis (letter). Aliment
Pharmacol Ther 2004;20(6):697-8.
2. Gallo-Torres H, Brinker A, Avigan M. Alosetron: ischemic colitis and serious
complications of constipation. Am J Gastroenterol 2006;101(5):1080-3.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I have no financial interest in this work or subject area.
Review for 10.1186/1471-230X-12-170 (2012)

Reviewer's report
Title:Role of Vitamin K2 in Preventing the Recurrence of Hepatocellular
Carcinoma after Curative Treatment.A Meta-Analysis of Randomized Controlled
Trials.
Version: 1Date:12 May 2012
Reviewer: Masaki Kaibori
Reviewer's report:
Overall the manuscript was well written and results were described in detail, this
study has no problems.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Review for 10.1186/1471-230X-12-170 (2012)

Reviewer's report
Title:Role of Vitamin K2 in Preventing the Recurrence of Hepatocellular
Carcinoma after Curative Treatment.A Meta-Analysis of Randomized Controlled
Trials.
Version: 1Date:3 July 2012
Reviewer: Masataka MS Seike
Reviewer's report:
In this article, the author summarized previous 5 RCTs that examined the effect
of vitamin K2 in preventing the recurrence of HCC using meta-analysis. The
author concluded that the efficacy of vitamin K2 in suppressing HCC recurrence
at 1 year was not confirmed in this meta-analysis.
Major compulsory revision
1.The largest and most recent trial by Yoshida and colleagues was performed as
a clinical trial (multicenter, placebo-controlled, double-blind trial enrolling 548
patients) to judge the preventive effect of vitamin K2 on HCC recurrence because
the previous results reported by Mizuta, Kakizaki and Hotta had been
inconsistent. So it is not appropriate to discuss these four manuscripts as same
category. In Japan, a consensus has been reached about no efficacy of vitamin
K2 in suppressing HCC recurrence after the clinical trial. Therefore we don’t think
this meta-analysis leads to a new knowledge in this field.
Minor essential revisions
1.Figure 1 is missing
2.In the Risults, 11th paragraph, 4th line, 95%CI:0.28-0.128 is a typographical
error, which should be read as 0.28-1.28.
3.Table 2, Mizuka is a typographical error for Mizuta.
4.Reference 1, the details of the journal are missing.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-12-170 (2012)

Reviewer's report
Title:Role of Vitamin K2 in Preventing the Recurrence of Hepatocellular
Carcinoma after Curative Treatment.A Meta-Analysis of Randomized Controlled
Trials.
Version: 2Date:19 October 2012
Reviewer: Masataka MS Seike
Reviewer's report:
The manuscript has been revised well. I think this manuscript will be acceptable
after some corrections have been done.
Major Compulsory Revisions
1.In Abstract(Result), the sentence which “The corresponding absolute risk
reductions in participants taking Vitamin K were -0.13(95%CI,-0.32 to -0.06)for
recurrence of hepatocelluar carcinoma at 1 year” is confusing, since this result
has not been defined in the Result.
2. The authors use mixed the both “vitamin K” and “vitamin K2” throughout the
manuscript. I think better to replace the word "vitamin K" with "vitamin K2".
Minor Essential Revisions
1.There are some typographical errors and inappropriate signs as comma, period
, parentheses e.t.c, throughout the manuscript. Please check them.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-12-169 (2012)

Reviewer's report
Title:Marginal turbid band and light blue crest, signs observed in magnifying
narrow-band imaging endoscopy, are indicative of gastric intestinal metaplasia
Version: 1Date:1 July 2012
Reviewer: Tiing Leong Ang
Reviewer's report:
This study examined the use of NBI magnifying endoscopy for diagnosis of IM.
Major comments
1. Methods (study population): why were patients on h2 antagonists or PPI
excluded? Why were patients with treated H pylori i9nfection treated?
2. Methods (endoscopic procedures): The MTB appears similar to LBC from the
image. It is not convincigly shown that this is a novel finding, and ot part of
spectrum of LBC.
3. Methods (endoscopic procedures): How many biopsies were taken at each
site? Was this standardized?
4. Results: Why were only 93 areas (not 94) evaluated? number of patietns was
47 and the plan was to evalaute the lesser and greater curve.
5.Results and discssion: are the endoscopic features (LBC/ MTB) evalauting IM
and atrophy? Or are they evaluating IM, and the detection of any atrophy a
reflection of the severity of the gastric mucosal inflmmation and change?
Minor comments
1. NBI is current ly no longer considered a noew or novel technology as it has
been in clincial use for many years. Hence the terms "new" and "newly
developed" should be deleted in the text.
2. There are some grammatical and typographical erros tat should be corrected.
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-12-169 (2012)

Reviewer's report
Title:Marginal turbid band and light blue crest, signs observed in magnifying
narrow-band imaging endoscopy, are indicative of gastric intestinal metaplasia
Version: 1Date:24 July 2012
Reviewer: Rungsun Rerknimitr
Reviewer's report:
- Major Compulsory Revisions
1. I am not quite sure about how the figures were displayed in the manuscript,
there must be some errors on figure labeling. Perhaps it may be, i.e. Figure
1C=Figure 3, Figure 1E=Figure 5. From what I saw in Figure 1C, LBC was also
present, but the author labeled it as “Regular honeycomb subepithelial network
and collecting venules subside. MTBs are seen (arrow), but LBC is not visible”.
This is the major pitfall of the present study since I cannot rely on the
interpretation of the difference between MTB and LBC for the accuracy of
predicting the presence of IM. In addition, the result of MTB reading by the author
(GH Kim) may be overlapping to the case where MTB was only interpreted but in
fact there might be LBC presented in that case as well. To solve this problem the
interobserver agreement is needed, before I can believe the accuracy of NBI
reading by a single interpreter.
2. IM usually locates in the antrum and body of the stomach. I wonder why the
examination was focused only at the lesser curvature of midbody and greater
curvature of upper body. Please explain.
3. In the background part paragraph#3, the authors stated “no study have
provided additional detail regarding the clinical significant….of LBC for predicting
IM” This is not true, there have been at least a few more publications since Udeo
published his first study in Endoscopy 2006. Please correct.
4. Please explain the technique of biopsy after magnifying NBI able to spot the
IM positive lesion, since switching the magnification back to a normal mode
before taking biopsy may be required. How did you do the mapping or make sure
that the biopsy was taken from the precise location?
5. MTB in your view may be the same as large long crest described by Bansal et
al (ref#8). Please explain the difference.
6. I am not quite sure about the availability of the magnify gastroscope
(GIF-H260Z) at other centers since it is not commercial available worldwide.
Therefore magnifying NBI is still reserved as a sophisticated technique in
advanced endoscopy center.
7. Please put all of the above mentioned into another paragraph as the limitation
of this study.
- Minor Essential Revisions
1. Figure labeling must be fixed.
2. In the results why there was only 46 specimens taken from the lesser
curvature instead of 47 (biopsy was taken from 47 patients).
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
We also published and still continue doing the research in this field.
But we do not have financial or non-financial competing of interests to this paper.
For the rest of other questions, the answer is "no".
Review for 10.1186/1471-230X-12-169 (2012)

Reviewer's report
Title:Marginal turbid band and light blue crest, signs observed in magnifying
narrow-band imaging endoscopy, are indicative of gastric intestinal metaplasia
Version: 2Date:23 August 2012
Reviewer: Rungsun Rerknimitr
Reviewer's report:
I am satisfied with the authors answers. Since they raise very important issue of
the possibility of the overlap in readings between MTB and LBC with an
interesting cartoon display. They should include these in their discussion to help
the readers better understand the new reading (MTB) for GIM.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
We also published and still continue doing the research in this field.
But we do not have financial or non-financial competing of interests to this paper.
For the rest of other questions, the answer is "no".
Review for 10.1186/1471-230X-12-169 (2012)

Reviewer's report
Title:Marginal turbid band and light blue crest, signs observed in magnifying
narrow-band imaging endoscopy, are indicative of gastric intestinal metaplasia
Version: 2Date:5 September 2012
Reviewer: Tiing Leong Ang
Reviewer's report:
The authors have attempted to answer all questions posed.
Major comments
1. Is the MTB really a novel fnding not commented on before? According to the
author’s endoscopic images, the authors are indicating the marginal epithelium
as MTB. Basically, normal (non-atrophic) body mucosa appears to have round
pits and circular marginal epithelium that was surrounded by network of
subepithelial capillary. When atrophy or intestinal metaplasia develops, the
epithelial structure changes to the pattern that the subepthelial capillary is
encased by surrounding marginal crypt epithelium (Bansal et al. GIE
2008;67:210-6; Kawamura et al. JGH, 2011;26:477-83). The latter looks similar
to the antral mucosa. I think the author is indicating the marginal crypt epithelium
in the antral type mucosa as MTB. This does not exist on the surface of the
epithelium and is the epithelium itself. So, it should not be given with the specific
name because this is not a specific appearance. This feature appear to have
been previously documetned by the two references mentioned here, although the
term MTB was not used. The morphological change of the epithelium occurred
prior to expression of brush border: the light blue crest.
2. METHOD, statistical analysis: The grade of gastritis should be treated as
categorical (non-numerical) variable because there is no continuity among
grades (none, mild, moderate and marked) of gastritis. Thus, it is better to
express with median (range or interquartile range) and to use non-parametric
analysis such as Wilcoxon’s rank test.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-12-169 (2012)

Reviewer's report
Title:Marginal turbid band and light blue crest, signs observed in magnifying
narrow-band imaging endoscopy, are indicative of gastric intestinal metaplasia
Version: 3Date:8 October 2012
Reviewer: Tiing Leong Ang
Reviewer's report:
The authors have answered the questions adequately.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-12-168 (2012)

Reviewer's report
Title:A Prospective Experimental study of liver fibrosis with ultrasound and Its
Correlation with hepatic reserve function and hemodynamics
Version: 1Date:14 February 2012
Reviewer: K-C Sudhamshu
Reviewer's report:
I have found the study interesting and it may add something in understanding the
hepatic hemodynamics in liver fibrosis. However, the manuscript needs revision
before it can be accepted for publication. Please consider following points.
Major comments:
1. Hepatic circulation index is not a widely used index. Even the author who
coined this index has not used this index in other articles from their group. So,
there should be reference for this index. Since same article has been used as
reference, it’s just matter of rearrangement.
2. Why prothrombin time was not measured as liver function? It is one of the
synthetic functions, as important as serum albumin.
3. Whether the USG operator was blinded with laboratory finding or not is
unclear. If not blinded there can be biasness.
4. In human, there is development of portal hypertension even in chronic
hepatitis stage i.e. pre-cirrhotic stage. After development in portal hypertension
there are changes in the hepatic circulation. Present study fails to elaborate and
discuss this issue.
5. In table 2 PVP has been taken as conventional liver function test. It is not true.
Minor points:
1. First sentence of second paragraph of discussion is unclear.
2. Language needs correction at places.
Review for 10.1186/1471-230X-12-168 (2012)

Reviewer's report
Title:A Prospective Experimental study of liver fibrosis with ultrasound and Its
Correlation with hepatic reserve function and hemodynamics
Version: 1Date:11 April 2012
Reviewer: Nigel Bird
Reviewer's report:
Major revisions
(1) This is an interesting paper but contains some major issues that require
resolution before it is acceptable for publication.
(1) the scoring system categorises fibrosis into 0, 1, 2, 3 and 4 but the authors
report only mild moderate and severe. There is no explanation for combining
categories 1 and 2; it is essential that this be justified.
(2) it is generally recognised that two independent, expert histopathologists score
the fibrosis separately and blinded to the origins of the samples and then reach
consensus on different scoring. Inter and intra-observer variability is too great to
ignore this. See Standish et al. 2006, Gut; 569-578
(3) the raw data for the groups of animals sacrificed at different time intervals
needs to be presented since there are clear overlaps in the degree of fibrosis
present at each time point.
Minor revisions
(1) References to the original paper reporting the development of the animal
model for fibrosis and the Xi'an scoring system need to be provided.
(2) What was the basis for the sample sizes? 11 for control group and 12 for the
other groups. Were power calculations or sample size calculations carried out?
(3) Since the fibrosis scores are categorical data the statement on pages 10 'A
better inverse correlation was found between HCI and ICG R15 (r = -0.890, p
<0.01) (Fig 3).' is incorrect, you cannot compare categorical data against
continuous data.
(4) I am not convinced that the liver function tests add anything to this paper.
They show what one would expect to find in animals that had been fed on a
hepatotoxic diet.
(5) The English is difficult to follow at times, some careful editing is need to be
done to address this.
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare no competing interests
Review for 10.1186/1471-230X-12-168 (2012)

Reviewer's report
Title:A Prospective Experimental study of liver fibrosis with ultrasound and Its
Correlation with hepatic reserve function and hemodynamics
Version: 3Date:27 July 2012
Reviewer: Nigel Bird
Reviewer's report:
The p value given for the ALT vs HCI seems to be wrong. The authors state that
the results were not significant but give a p value of 0.012 which does indicate
significance. Figure 8 also has the same value on it but there is clearly no
significant correlation.
The legend to Table is confusing and suggests that 11 animals with F1 were
sacrificed at 8 weeks and none after that. Could I suggest "Stage of liver fibrosis
at different time intervals." or something like that.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-12-168 (2012)

Reviewer's report
Title:A Prospective Experimental study of liver fibrosis with ultrasound and Its
Correlation with hepatic reserve function and hemodynamics
Version: 3Date:2 August 2012
Reviewer: K-C Sudhamshu
Reviewer's report:
I could not see the reply to my comments. However, while going through the
manuscript it seems that some points are clarified and manuscript is revised. Is it
possible to ask for the reply to comments and revised manuscript indicating the
changes that have been made?
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-12-167 (2012)

Reviewer's report
Title:Association of genetic variations in GNB1 with response to peginterferon
plus ribavirin therapy for chronic hepatitis C in a Chinese population in Taiwan
Version: 1Date:27 August 2012
Reviewer: Claudio Puoti
Reviewer's report:
This is an interesting paper aimed at evaluating whether polymorphisms in the
GNB1 gene are associated with a RVR among HCV-1 and HCV-2 infected
patients receiving peginterferon plus ribavirin treatment (PEG-IFN -RBV). The
main conclusion of this study is that GNB1 polymorphisms might be associated
with the therapeutic outcomes of HCV-1 and HCV-2 infected patients under
standard of care treatment.
This issue is interesting and rather innovative, as the authors did evaluate the
association between single nucleotide polymorphisms (SNPs) in the GNB1 gene
and their susceptibility to RVR in Chinese patients in Taiwan receiving PEG-IFN
-RBV treatment.
The paper is well written and the patient series is huge (265 HCV-1 infected
patients and 195 HCV-2 infected patients), so I have only few comments.
MAJOR COMMENTS
1. The main pitfall of this study is that no information about liver histology or liver
fibrosis by non-invasive methods is given. The lack of these data strongly
decrease the strength of the work. In other words, the higher response rate found
among some HCV-1 and HCV-2 patients might theoretically be due to a lower
fibrosis degree in these sub-groups rather than to GNB1 polymorphisms.
2. How many flat responders were seen among non-RVR patients, and did they
differ according to GNB1 polymorphisms?
3. Recent guidelines (for example, see EASL Clinical Practice Guidelines:
Management of hepatitis C
virus infection, J Hepatol 2011) suggest that patients with HCV genotypes 1
should receive a weight-based dose of ribavirin of 15 mg/kg body weight per day.
In this study, patients > 80 kg received a maximum RBV dose of 1000 mg/day,
that might justify the absence of RVR in some HCV-1 patients.
MINOR COMMENTS
1. Further data on patient features should be added in table 1 (ALT levels, PLT
count, etc)
2. Were IL28b polymorphisms available in this series of patients ? is so, I
strongly suggest to add these results.
3. the authors should specify that patients were treated with PEG IFN alfa 2b.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
CLAUDIO PUOTI, MD
LIVER UNIT, MARINO, ROMA, ITALY
Review for 10.1186/1471-230X-12-167 (2012)

Reviewer's report
Title:Association of genetic variations in GNB1 with response to peginterferon
plus ribavirin therapy for chronic hepatitis C in a Chinese population in Taiwan
Version: 1Date:24 September 2012
Reviewer: Mahmoud Khattab
Reviewer's report:
Comments to authors:
1Major Comulsory Revision:-In discussion,you have presented a paragraph
discussing data concernedwith your study resuls regarding SVR in both HCV-1
and HCV-2,and you mentioned that there was no correlation between
polymorphism in GNB1,the gene you have studied and SVR.Then why have you
adressed your artcle by:
impact of this gene on RVR?and then presenting evidence that RVR predicts
SVR to justify your preliminary results concerning confusing relations between
GNB1 gene polymorphism.
2-Major Comulsory Revision:-When a clinician tries to read your manuscript he
will be confused by the way you have presented and discussed your data.for
example,you mentioned that the distribution of different alleles was not different
from RVR(+)and
RVR(-) Patients,and then you stated that thedosage effect of Gallele at
rs12126768 was inversely correlated to RVR in HCV1.
What is meant by dose effect?,Have this any value? you have not explained all
these questions in discussion.
3-Major Compulsory Revision:There is much overlap in the manuscript by using
numbers rather than letters(A,C,G,T) to indicate the individual alleles,it was more
simplified towrite in the letter form.
4-Minor Revision:-What is meant by GNB1 halotype?and what is its
significance?in relation to prediction of response.
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-12-167 (2012)

Reviewer's report
Title:Association of genetic variations in GNB1 with response to peginterferon
plus ribavirin therapy for chronic hepatitis C in a Chinese population in Taiwan
Version: 2Date:4 November 2012
Reviewer: Claudio Puoti
Reviewer's report:
The paper has been substantially modified according to Reviewers' suggestions,
and its interest did greatly improved. The revised version is more clear and thus I
believe that the work is now worthy to be published in BMC Gastroenterology.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
CLAUDIO PUOTI, MD
Review for 10.1186/1471-230X-12-166 (2012)

Reviewer's report
Title:IgG and IgG4 antibodies in subjects with irritable bowel syndrome: a case
control study in the general population
Version: 1Date:2 July 2012
Reviewer: Lena Öhman
Reviewer's report:
In this paper, the authors aimed to compare IgG and IgG4 food and yeast
antibodies in subjects with and without IBS. Blood samples were collected, and
IgG and IgG4 food and yeast antibodies were measured in 269 subjects with IBS
and 277 control subjects. All subjects completed questionnaires.
This is an interesting and important paper, trying to reveal whether IgG and IgG4
food and yeast antibodies are associated with IBS.
General comments
It is unclear how gastrointestinal symptoms were assessed. This ought to be
described in detail. Also the questions regarding food and drink ought to be
described in some detail, although these have been described in a previous
paper.
The ELISA analysis of IgG and IgG4 antibodies should be described in more
detail; at least manufacturer and detection limits ought to be given.
Supposedly the subjects self-estimated their food intake; it may be discussed
whether this method may affect the results. What is the correlation and /or
difference between self-estimated food intake and a food diary?
Will serum levels of food specific antibodies be the best way to determine food
intolerance? What about specific antibodies in fecal samples or mucosal
biopsies? What about sensitivity of available assays?
Many readers would benefit from an introduction to why the IgG4 subclass is
interesting to measure. It is also unclear from the paper why Candida albicans is
related to sugar.
The “multiple imputation” used to handle missing values also need to be
described in more detail.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'