JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-9-40 (2009)

Reviewer's report
Title:Afferent signalling from the acid-challenged rat stomach is inhibited and
gastric acid elimination is enhanced by lafutidine
Version: 1Date:17 March 2009
Reviewer: Benedicte De Winter
Reviewer's report:
The manuscript describes the effects of lafutidine on acid-induced afferent
signalling to the brainstem, mucosal injury, intragastric acidity and gastric
emptying concluding that lafutidine has protective effects apart from its ability to
suppress gastric acid secretion. The authors describe an increase in intragastric
pH that might be related to either dilution and/or to acceleration of gastric
emptying. However, the mechanism of action and the distinct role of these two
potential mechanisms is not unravelled.
major remarks
1. The results and conclusion are largely based on the c-Fos experiments and
the estimate of gastric emptying. However, I do have some methodological
concerns. The decrease in c-FOS immunoreactivity is small and reaches only
statistical significance if the authors assume that a p-value of 0.1 is significantly
different. As this forms the basis of the hypothesis concerning the effects of
lafutidine on vagal afferent activity, we suggest to increase the number of rats
(despite the exploratory nature of the study) to be able to draw firm conclusions.
It would also be interesting to show a picture of the c-Fos immunoreactivity in
control rats to be able to compare the results.
2. I also wonder why the authors used the weight of the gastric content as an
indirect technique to measure gastric emptying. It would be interesting to
measure gastric emptying as a direct parameter to support the hypothesis on the
accelerating effect of lafutidine on gastric emptying firmly. In my view, the use of
this technique makes it hard to distinguish between an effect on dilution and on
gastric emptying per se. The technique with the solid beads could help to
distinguish between both parameters.
3. In the methodology on the determination of the gastric volume a second
analysis is used expressing the gastric volumes at time 60 and 120 min relatively
to time 0. As there is a difference in the values of the gastric volume in the
lafutidine- and cimetidine-treated rats at time 0, we wonder whether this
methodology can be used.
4. Does lafutidine has an effect per se on any of the parameters measured?
Does lafutidine for instance has an effect on gastric emptying in control rats?
These control experiments are lacking.
5. The authors compare the potency of lafutidine to cimetidine in the second
set-up of experiments. The effects of cimetidine are less pronounced. We wonder
whether this could be related to the different dose that was used for cimetidine
(10 mg/kg) whereas in these experiments lafutidine was used in the higher dose
of 30 mg/kg.
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 declare that I have no competing interests'
Review for 10.1186/1471-230X-9-40 (2009)

Reviewer's report
Title:Afferent signalling from the acid-challenged rat stomach is inhibited and
gastric acid elimination is enhanced by lafutidine
Version: 1Date:23 March 2009
Reviewer: Kenji Okajima
Reviewer's report:
The authors compared the effects of lafutidine and cimetidine on acid-induced
vagal sensory signaling to the brain stem, the gastric mucosal injury, intragastric
acidity and gastric emptying after gastric acid challenge in rats. Acid-induced
vagal afferent signaling was inhibited by these two drugs. However, laftudidne
exerted the gastroprotective effect in pararell with facilitation of gastric emptying
and a reduction of gastric acidity more markedly than cimetidine.The authors
concluded that sensory neuron stimulatory activyt of lafutidine might explain such
a difference observed between these two H2RAs in this animal model.
Major revisions:
Although observations are somewhat interesting, evidence support for the
mechanistic insight the authors made in the paper should be necessary. Major
revisoin providing data supproting the involvement of sensory neurons in
lafutidine-induced events should be done.
Gastric levels of CGRP and prostaglandins (6-keto PGF1a and PGE2) should be
determined after acid and/or drugs. Effect of TRPV 1 antagonists on facilitation of
gastric emptying and a reduction of gastric acidity in animals given these two
drugs.
Minor revisions:
Data obtained in animals given cimetidine should also be described in the
Abstract section.
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-9-40 (2009)

Reviewer's report
Title:Afferent signalling from the acid-challenged rat stomach is inhibited and
gastric acid elimination is enhanced by lafutidine
Version: 2Date:5 May 2009
Reviewer: Koji Takeuchi
Reviewer's report:
I have read through the revised manuscript as well as the author’s response to
the reviewer’s inquiries, and found that the authors extensively and successfully
revised the paper by taking the reviewer’s comments into consideration. I also
checked whether the authors revised the text upon considering the comments of
Reviewers 2 and 3. Although the authors did not provide any new data to support
their contention or to refute the reviewer's comments, the responses to their
comments are all nicely accepted. Overall, I think, this paper at its present form is
now recommended for publication in BMC Gastroenterology.
Review for 10.1186/1471-230X-9-40 (2009)

Reviewer's report
Title:Afferent signalling from the acid-challenged rat stomach is inhibited and
gastric acid elimination is enhanced by lafutidine
Version: 2Date:20 May 2009
Reviewer: Benedicte De Winter
Reviewer's report:
The authors addressed the topics raised by the three reviewers sufficiently in the
manuscript: they clarified some aspects and put other aspects into a broader
perspective, discussing the advantages and disadvantages of the model used
into more detail (for instance the indirect method used to give an appraisal on
gastric emptying).
However, they did not perform the additional experiments asked by the referees
due to several reasons such as the leaving of the PhD student and concerns of
the Ethical committee. I do have a remark concerning the ethical considerations:
I do agree that the amount of animals used should be as low as possible
certainly in experiments involving a pain stimulus. On the other hand it seems
very unethical to me to perform these experiments in a number of animals that is
too small to allow the study design to represent enough power to detect
differences. An underpowered study will not allow any conclusions at all and
therefore I feel that the rats used in such a protocol are wasted anyway.
Therefore a statement as “maximal 6 rats in a group” seems not scientifically
valid to me.
The control experiments we indicated refer to experiments in animals treated with
vehicle or lafutidine without the acid challenge in order to investigate the effects
of the drugs in basal conditions for instance on c-FOS expression and gastric
emptying or secretion. For the c-FOS experiments this would allow the readers to
confirm themselves the absence of c-FOS staining in non-challenged rats and
the increase obtained by acid challenge, for the gastric emptying studies it would
allow to investigate the presence/absence of an effect of lafutidine per se on
gastric emptying (without the acid challenge). These controls seem valuable to
us since they offer the possibility to further investigate the pathogenetic
mechanisms involved in control conditions versus a condition of gastric acid
challenge.
Concerning the lower dose of cimetidine compared to lafutidine I suggest to
include this dose difference also in the discussion on page 16, it might represent
another explanation for the less pronounced effect of cimetidine.
Benedicte De Winter
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-9-39 (2009)

Reviewer's report
Title:Induction of G1 and G2/M cell cycle arrests by the dietary compound
3,3'-diindolylmethane in HT-29 human colon cancer cells
Version: 1Date:11 January 2009
Reviewer: Thomas Szekeres
Reviewer's report:
Induction of G1 and G2/M cell cycle arrests by the dietary compound 3, 3’
diindolylmethane in HT-29 human colon cancer cells by Choi et al.
The authors describe the effects of 3, 3’ diindolylmethane on the cell cycle
progression in human colon cancer cells (HT-29). The data and results presented
are interesting, however I would suggest extending this study and including
additional results, as the results presented are describing the effects of one
compound in one cell line at one concentration. The concentration of 30 uM used
for the experiments is 10 times higher than the concentration which can be
achieved and therefore additional data are necessary to draw the conclusions
stated by the authors. I would suggest including results with lower concentrations
prior to publication of this manuscript.
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.
Review for 10.1186/1471-230X-9-39 (2009)

Reviewer's report
Title:Induction of G1 and G2/M cell cycle arrests by the dietary compound
3,3'-diindolylmethane in HT-29 human colon cancer cells
Version: 1Date:2 February 2009
Reviewer: Farrukh Afaq
Reviewer's report:
In this study, the authors examined the effect of 3,3’-diindolylmetnane (DIM) on
cell cycle progression in HT-29 cells. This study is an extension of the previous
work in which the authors have shown that DIM inhibited the growth of colon
cells. Here, the authors further suggest that treatment of cells with DIM resulted
in a dose-dependent reduction in DNA synthesis. Furthermore, the percentage of
cells in G1 and G2/M phases were significantly increased after DIM treatment
and this was accompanied by reduced expression cyclins and cdk4 an increased
expression of p21 1nd p27. This is an interesting study and the experiments
appear to be well-planned and conducted. There are some concerns which are
listed below:
The authors should also provide dose-dependent data to further prove that DIM
treatment resulted in G1 and G2/M phase arrest.
The authors should also examine the effect of DIM on normal cells?
Since the expression of p21 is tightly regulated by p53, the authors are
encouraged to examine the status of p53 after DIM treatment.
What was the effect of DIM on p16 expression?
Some of the sentences in the manuscript are difficult to understand and need
rephrasing.
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.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-39 (2009)

Reviewer's report
Title:Induction of G1 and G2/M cell cycle arrests by the dietary compound
3,3'-diindolylmethane in HT-29 human colon cancer cells
Version: 5Date:7 May 2009
Reviewer: Thomas Szekeres
Reviewer's report:
The manuscript is acceptable in its form for publication
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.
Review for 10.1186/1471-230X-9-39 (2009)

Reviewer's report
Title:Induction of G1 and G2/M cell cycle arrests by the dietary compound
3,3'-diindolylmethane in HT-29 human colon cancer cells
Version: 5Date:7 May 2009
Reviewer: Farrukh Afaq
Reviewer's report:
NONE
Level of interest: An article of outstanding merit and interest 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-9-38 (2009)

Reviewer's report
Title:High efficacy in Helicobacter pylori retreatment: seven days with
furazolidone, levofloxacin and lansoprazole, in Sao Paulo, Brazil.
Version: 2Date:21 November 2008
Reviewer: V Ahuja
Reviewer's report:
This is a well conducted study which looks at the efficacy and tolerability rates of
a furazolidone salvage therapy . This may be a pertinent question to be
answered as the number of H.pylori eradication failures are on the rise in
developing countries. Hence there is a need to test various salvage therapies
which are not affected by metronidazole as we as clarithromycin resistance .
Major problems with this study :
<!--[if !supportLists]-->1. <!--[endif]-->Antibiotic sensitivity tests on gastric
biopsies have not been conducted .
<!--[if !supportLists]-->2. <!--[endif]-->The sample size is not large
The authors need to discuss these two major limitations of this study in the
Discussion section.
Minor problems :
<!--[if !supportLists]-->1. <!--[endif]-->It is not clear as on what basis the
investigators decided to give the therapy for 7 days and not ten days or 14 days .
The investigators should discuss the previously published literature on
furazolidone based therapies and the impact of therapy duration.
<!--[if !supportLists]-->2. <!--[endif]-->It would be interesting to know what was the
status of urease based tests versus histology in determining eradication status
As eradication status was defined as 2of 3 tests negative . Is it possible that
eradication rates were overestimated in case there was a skew of urease based
tests being negative as opposed to histology ? This is a well described
phenomenon which may occur particularly in situations where H.pylori density is
low.
<!--[if !supportLists]-->3. <!--[endif]-->Table 6 should be described in greater
detail in Results section
<!--[if !supportLists]-->4. <!--[endif]-->Table 5 may be deleted
<!--[if !supportLists]-->5. <!--[endif]-->Table 2 : the activity scale has not been
mentioned in methods section
Review for 10.1186/1471-230X-9-38 (2009)

Reviewer's report
Title:High efficacy in Helicobacter pylori retreatment: seven days with
furazolidone, levofloxacin and lansoprazole, in Sao Paulo, Brazil.
Version: 3Date:16 January 2009
Reviewer: Ala I Sharara
Reviewer's report:
The authors have addressed most of the concerns raised. However, the following
issues require additional clarifications and modifications. The authors have failed
to properly address one of the raised points (see below). Their response that
“The treatment schemes used in these patients already tested in our service
have shown fewer efficacies (4, 7 e 8). A Brazilian Helicobacter pylori sensibility
study showed a 13% furazolidone primary resistance (3). In another study (9),
the secondary furazolidone resistance was also low.” does NOT answer the
query on the eradication rate of patients who had previously failed one or more
furazolidone-containing regimen(s).
Major issues:
1. From table 2 (Table 3 in the first submission), it appears that 15 patients had
previously failed one (or more in the case of 2 patients) furazolidone-containing
regimen. It is therefore important to examine the eradication rate in such patients
compared to furazolidone-naïve patients. Moreover, 3 patients received “other”
regimens under the 3 or more prior regimen category. If any of those had
received furazolidone in the past, they need to be added to the analysis of the 15
listed above.
2. The discussion is very disjointed and needs to be rewritten as distinct
paragraphs addressing distinct points
Level of interest: An article whose findings are important to those with closely
related research interests
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-9-38 (2009)

Reviewer's report
Title:High efficacy in Helicobacter pylori retreatment: seven days with
furazolidone, levofloxacin and lansoprazole, in Sao Paulo, Brazil.
Version: 4Date:6 April 2009
Reviewer: Ala I Sharara
Reviewer's report:
The authors have addressed the raised concerns satisfactorily. The discussion is
better articulated although it could still use some editorial changes to ensure
proper English and structure.
Minor essential issues:
1. I suggest that the title of the article be changed to: Efficacy of a 7-day course
of furazolidone, levofloxacin, and lansoprazole after Failed Helicobacter pylori
Eradication
2. The authors should avoid stating that the H. pylori in their patients was
“resistant” since they did not perform in vitro susceptibility testing. They should
instead replace it with persistent. For instance, in the abstract, replace “ in
patients with resistant H. pylori Infection” by “in patients with persistent H. pylori
infection”.
3. It would be helpful to include the following in the results section of the abstract:
“Compared to furazolidone-naïve patients, eradication rates were inferior in those
who had failed prior furazolidone-containing regimen(s) (74% vs. 100%,
p=0.002)”
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.
Declaration of competing interests:
'I declare that I have no competing interests
Review for 10.1186/1471-230X-9-37 (2009)

Reviewer's report
Title:Polymorphism in COX-2 modifies the inverse association between
Helicobacter pylori seropositivity and esophageal squamous cell carcinoma risk
in Taiwan: a case control study
Version: 2Date:2 April 2009
Reviewer: Sara Raimondi
Reviewer's report:
I am happy with the revisions made. I think the paper is now suitable for
publication.
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-9-36 (2009)

Reviewer's report
Title:Antiulcer activity of fluvoxamine in rats and its effect on oxidant and
antioxidant parameters in stomach tissue
Version: 2Date:12 January 2009
Reviewer: Jonathan Kaunitz
Reviewer's report:
Using a standard rat indomethacin ulcer model, the authors report the
fluvoxamine, a drug used in the treatment of obsessive-compulsive disorder,
prevents acute ulcer formation. Furthermore, the drug appears to have
anti-oxidant effects, increasing the production of NO and GSH, while diminishing
the production of MDA and MPO.
Major Compulsory Revisions:
1. The doses of fluvoxamine used (50-200 mg/kg) are far greater than those
used clinically, (1-5 mg/kg). The authors should hence point this out and interpret
their rat data with far more caution, avoding speculation about clinical translation.
2. Fluvoxamine is a CYP 1A2 inhibitor. CYP 1A are believed to generate ROS
(Cf. Mol Pharmacol. 1999 Sep;56(3):588-97) Could this be a possible
explanation for the data shown?
3. The data are depicted in a non-standard, redundant, and somewhat confusing
fashion. It is not necessary to have numerical data in the text and again in a
graph. Please add error bars to the graphs and omit the data from the text.
Furthermore, the data are described in the Results section in an order different to
what is shown in the graphs. Moreover, the use of the terms “intact” is confusing.
Suggest a row for indo, fluvoxamine and ranitidine dose under each graph, with
numbers representing the dose.
4. The figures with the gastric mucosa depict standard results and thus should be
deleted.
5. Please remove unsupported statements such as “The clinical efficacy of
antidepressant drugs…” on the 1st page of the Introduction.
6. Is distilled water the correct vehicle control?
7. Is it correct to statistically compare the “intact” (no indo) with the control
(indo)?
8. The second half of the 1st paragraph if the Discussion does not bear on the
data and should be deleted.
9. The last sentence of the text should be deleted.
Minor Essential Revisions:
1. Capitalization: Helicobacter
2. Please correct and edit for proprper English usage
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.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-36 (2009)

Reviewer's report
Title:Antiulcer activity of fluvoxamine in rats and its effect on oxidant and
antioxidant parameters in stomach tissue
Version: 3Date:25 March 2009
Reviewer: Predrag Sikiric
Reviewer's report:
Generally, the manuscript is now considerably improved and all of my previous
comments were adequately solved.
However, the only point that I could object is the statement that ranitidine was
evaluated as an ulcerogenic agent (!) (i.e., Abstract:
„Methods: Groups of rats fasted for 24 h received fluvoxamine (25, 50, 100 and
200 mg/kg), ranitidine (50 mg/kg) or distilled water by oral gavage.
Indomethacin (25 mg/kg) was orally administered to the rats as an ulcerative
agent. Six hours after ulcer induction, the stomachs of the rats were excised and
an ulcer index determined. Separate groups of rats were treated with the same
doses of fluvoxamine and ranitidine, but not with indomethacin, to test for
ulcerative effects of these drugs alone. The stomachs were evaluated
biochemically to determine oxidant and antioxidant parameters. We used
one-way ANOVA and LSD options for data analysis. Results: The 25, 50, 100
and 200 mg/kg doses of fluvoxamine exerted antiulcer effects of 48.5, 67.5, 82.1
and 96.1%, respectively, compared to the control rat group. Ranitidine showed
an 86.5% antiulcer effect. No ulcers were observed in the absence of
indomethacin treatment for any dose of fluvoxamine or for ranitidine.
….“ Results: The antiulcer effect of 50 mg/kg ranitidine was 86.5%. No ulcers
were observed in the absence of indomethacin treatment following any dose of
fluvoxamine or ranitidine.“).
Thus, although the intention of the authors is clear, the idea that ranitidine may
induce ulcer by itself is quite unusual, and the above statements should be
adequately corrected.
The same goes for fluvoxamine. If they authors think that fluvoxamine may
produce ulcer by itself, and then, protect against indomethacin lesion, they
should provide some background (i.e., small irritant may protect against strong
irritant).
Finally, providing that this technical point could be solved without problem, I
maintained my previous high estimation of this very interesting manuscript that
deserves full attention and presentation.
Review for 10.1186/1471-230X-9-36 (2009)

Reviewer's report
Title:Antiulcer activity of fluvoxamine in rats and its effect on oxidant and
antioxidant parameters in stomach tissue
Version: 3Date:31 March 2009
Reviewer: Jonathan Kaunitz
Reviewer's report:
General:
The authors resubmitted a manuscript in which they report that the compound
fluvoxamine, clinically used as an antidepressant, at high doses impairs gastric
ulceration in a standard indomethacin rat model.
The authors have conducted new studies in order to address concerns raised in
the critiques.
Major Compulsory Revisions:
Please provide more details regarding the GSH, NO, MPO, and MDA assays.
Simply stating that the samples were "sent to a biochemistry laboratory" was no
adequate.
Minor Essential Revisions:
Please explain abbreviations: LSD, MAO-B, GIS, etc.
Please use consistent spelling e.g. fluvoxamine, leukotriene, polymorph
Discretionary Revisions: None
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.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-34 (2009)

Reviewer's report
Title:Macroscopic Extent of Gastric Mucosal Atrophy: Increased Risk Factor for
Esophageal Squamous Cell Carcinoma in Japan
Version: 1Date:24 March 2009
Reviewer: Elfriede Bollschweiler
Reviewer's report:
Review for BMC gastroenterology
Title: Macroscopic Extent of Gastric Mucosal Atrophy: Increased Risk Factor for
Esophageal Squamous Cell Carcinoma in Japan.
Authors: Tomoyuki Akiyama et al.
The above mention manuscript is a case-control study analyzing the
macroscopic extent of gastric mucosal atrophy as risk factor for esophageal
squamous cell carcinoma. The authors compared the endoscopic figures of 253
patients with esophageal cancer with those of 253 age- and sex matched
controls. The results show very clearly the relations between gastric atrophy and
esophageal cancer . The paper is well written and the statistic is adequate for
this question.
My conclusion, this is a good manuscript with an interesting topic and should be
published.
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-9-34 (2009)

Reviewer's report
Title:Macroscopic Extent of Gastric Mucosal Atrophy: Increased Risk Factor for
Esophageal Squamous Cell Carcinoma in Japan
Version: 1Date:29 March 2009
Reviewer: Theodore Rokkas
Reviewer's report:
This is an interesting paper which might have practical implications in identifying
people at high risk for ESCC, provided that other studies will confirm their data.
The only minor point is that the authors should include in their discussion a
recent meta-analysis, "Rokkas T et al: Relationship between Helicobacter pylori
infection and esophageal neoplasia: A meta-analysis. Clin Gastroenterol Hepatol
2007;5:1413-1417" in which no relationship was found between ESCC and
Helicobacter pylori infection (including the Cag A status).
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.
Review for 10.1186/1471-230X-9-33 (2009)

Reviewer's report
Title:Food allergy alters jejunal circular muscle contractility and induces local
inflammatory cytokine expression in a mouse model
Version: 1Date:23 November 2008
Reviewer: Hirotada Akiho
Reviewer's report:
Comments to Authors
The experiments are carefully performed and the manuscript has implications for
investigators in the fields of both motility and inflammation.
Minor comments
#1 Results
Page 11, cytokine expression
Do you have any data for cytokine expression in circular muscle alone?
If not, you should mention about how local Th2 cytokines affect the circular
muscle contractility in discussion. (e.g. Macrophage, Zhao A et al.
Gastroenterology 2008, 5-HT, Motomura Y et al. Gut 2008)
#2 Page 11, smooth muscle contractility
It is worthwhile to look at the ileal smooth muscle contractility.
#3 Page 22
Table 1
You should delete the results of 1:20 dilution.
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.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-33 (2009)

Reviewer's report
Title:Food allergy alters jejunal circular muscle contractility and induces local
inflammatory cytokine expression in a mouse model
Version: 2Date:27 March 2009
Reviewer: Eva Untersmayr
Reviewer's report:
The authors have thoroughly revised their manuscript according to the reviewers’
suggestions.
Nevertheless, I would recommend one additional major compulsory revision: Not
only in the text but also in the figures mean +/- SD should be given as the
standard error of the mean (SEM) is the standard deviation of the error in the
sample mean relative to the true mean and thus does not provide enough
statistical information.
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.
Review for 10.1186/1471-230X-9-33 (2009)

Reviewer's report
Title:Food allergy alters jejunal circular muscle contractility and induces local
inflammatory cytokine expression in a mouse model
Version: 2Date:31 March 2009
Reviewer: Gabriella Di Felice
Reviewer's report:
The authors have satisfactorily addressed the issues I raised in my original
review of this manuscript, and I have no further comments.
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-9-35 (2009)

Reviewer's report
Title:Socioeconomic status and mortality among cirrhosis patients: A Danish
nationwide cohort study
Version: 1Date:28 January 2009
Reviewer: Pia Makela
Reviewer's report:
The paper by Jepsen et al. is a high-quality study on an interesting, focused
subject. They set out to study how certain sociodemographic factors (marital
status, income, employment) affect survival of cirrhosis patients. This is a
worthwhile subject to study. They have the best possible data for studying this
research question, with the confounding factors and other variables selected with
care and expertise. They use appropriate methodology, and their analyses give
the answer to the question they posed. The text is well written and the language
is good. I have only minor comments to the authors.
Minor essential revisions
As there is no lack of space, and the analyses are simple and straight-forward,
there is no reason not to show the rest of the parameter estimates from the
estimated models now shown in Table 2 (the different indicators of cirrhosis
severity, gender, age, substance use diagnosis, comorbidity). Many of them
would be of equally high interest as those that are in the focus of the paper.
The logic is unclear in the sentence on p. 10 "The lack of data on socioeconomic
status at the time of cirrhosis diagnosis is another weakness because the
socioeconomic information from the calendar year before cirrhosis diagnosis
might have been affected by an already established cirrhosis, or it might have
predated the cirrhosis by up to one year". If the sociodemographic data from year
before cirrhosis diagnosis may have been affected by the cirrhosis diagnosis,
then the sociodemographic data at the time of the diagnosis may be even more
affected, and the data should rather come from previous years (which data the
authors have) rather than more recent times.
Discretionary revisions
Would "sociodemographic" be a better term for the three variables studied than
"socioeconomic", which most often is used to refer to income, education and
occupation?
Additional
The authors might find of interest a related article by the referee: Mäkelä P et al.
(2003) What underlies the high alcohol-related mortality of the disadvantaged:
high morbidity or poor survival? Journal of Epidemiology and Community Health
57:981-986.
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-9-35 (2009)

Reviewer's report
Title:Socioeconomic status and mortality among cirrhosis patients: A Danish
nationwide cohort study
Version: 1Date:20 February 2009
Reviewer: Mats Ramstedt
Reviewer's report:
General remarks
This study addresses the question of whether low socioeconomic status is
associated with worse prognosis after cirrhosis diagnosis, which has been found
for several other alcohol-related diseases. As indicators of socioeconomic status
the authors use marital status, employment and personal income.
In order to examine this question, a population based cohort study with 5-year
follow up of 1765 Danish cirrhosis patients diagnosed in 1999-2001 was
conducted. Estimation of Cox-regression models (controlling for substance
abuse, co-morbidity etc.) showed that being divorced and a disability pensioner
were significantly associated with lower survival after 5 years but not
unemployment and low income.
To reveal a prognostic value of some socioeconomic conditions is certainly
valuable information and the statistical analysis seems sound. A weakness of the
study is however that the mechanisms behind these statistical associations
remain unclear, and that a theoretical rationale for assuming a link between
socioeconomic status is missing or is at least rather weak.
Major comments
" A definition of the concept socioeconomic status is lacking as well as a
discussion of how it is assumed to affect the likelihood of survival after cirrhosis
diagnosis. In what respect is marital status a socioeconomic condition and what
is the connection with social support (as it is called in the discussion, p 11)?
" The findings indicate that something about being divorced and being disabled
worsens the prognosis for cirrhosis patients but the authors fail to bring up
possible mechanisms except from the possibility that they would be "less
compliant with doctors advice to stop drinking" and then some general
statements of "range of behavioural, psychological, social and biological
mechanisms..". It seems that some more ambitious attempts to explain the
results are warranted, e.g. the general state of health (mental and somatic)
compared to the other groups?
Minor comments
" None of the studies cited for the statement that there is link between low
socioeconomic status and cirrhosis are based on Danish data. If this has not
been examined previously with Danish data that could be stressed as a rationale
for this study, not the least since the Danish welfare system aims at reducing
socioeconomic deífferences in health.
" The cause of death during follow-up would have been interesting information,
why was that not reported?
" The income measure was fairly rough; were there any indications that a more
detailed measure would have changed the importance of income, which
appeared important in other studies?
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 interest
Review for 10.1186/1471-230X-9-31 (2009)

Reviewer's report
Title:Meta-analysis of Percutaneous Radiofrequency Ablation versus Ethanol
Injection in Hepatocellular Carcinoma.
Version: 1Date:19 January 2009
Reviewer: Kazutaka Kurokohchi
Reviewer's report:
Review RE: Meta-analysis of percutaneous radiofrequency ablation versus
ethanol injection in hepatocellar carcinoma by Bouza et. al.
The authors analyzed systemic reviews and meta-analyses of randomized
control trials of hepatocellular carcinoma treated with RFA and PEI and
concluded that RFA is superior to PEI in terms of better survival and local control
of disease. However, the higher rates of adverse events are displayed in the RFA
treatment.
Analyzed systematic reviews are appropriately selected. Both of method for
analysis and analyzed item focused on are also appropriate. Therefore, this
manuscript should be finally published in the BMC Gastroenterology.
Although it is mentioned in the manuscript regarding the adverse effects of RFA
and PEI, those effects on the hepatic capacity are not mentioned. As everyone
knows, RFA treatment sometimes affects hepatic capacity of cirrhotic liver
leading to decrease of the level of albumin and administration of amino acids is
helpful to prevent the decrease of albumin level. Thus, it is likely to be better to
address regarding the effect of RFA on the hepatic capacity somewhere in the
manuscript.
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-9-31 (2009)

Reviewer's report
Title:Meta-analysis of Percutaneous Radiofrequency Ablation versus Ethanol
Injection in Hepatocellular Carcinoma.
Version: 1Date:21 January 2009
Reviewer: Franco Brunello
Reviewer's report:
No major compulsory revision
Minor essential revisions:
page 2 line 13 -14 by instead of with
line 24 in terms of better....
page 3 line 6 HCC can be offered instead of offers
line 20 about instead of as to
line 26 of the relevant references was made...(inversion of the verb)
page 4 line 2 related instead of relating
line 8 selected studies (not located)
page 5 line 9 by instead of with (two times)
page 6 line 13 -14 by instead of with
page 7 line 18 in RFA group vs PEI
page 8 line 3 has instead of had
page 8 line 7 data are not data is
line 9 higher than that...
line 12 this istead of its
line 29 and we are confident that the majority...
page 9 line 21 in terms of better
Discretionary revisions: the authors could explain that the health policy in
different countries is different and the mean Hospital stay and the costs of RFA
versus PEI are not easily comparable. In fact in Europe PEI is performed as
ambulatory or Day Hospital service whereas in Japan PEI is offered during
Hospital staying.
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: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interest.
Review for 10.1186/1471-230X-9-31 (2009)

Reviewer's report
Title:Meta-analysis of Percutaneous Radiofrequency Ablation versus Ethanol
Injection in Hepatocellular Carcinoma.
Version: 1Date:2 February 2009
Reviewer: Guy J Maddern
Reviewer's report:
Limited data available.
Good effort to compile and analyse the data.
The quality of the studies included was a bit difficult to guage, most included
patients who appear suitable for a liver resection/trasplant (74% Childs A, 57%
solitary, mean size 2.5cm).
Perhaps the autors can clarify why these were irresectable.
The studies included are very expectedly heterogenous, but RFA results appear
unquestionably better.
Reproducible
Well written - should use more headings and subheadings especially in results
category eg. A)Safety
i) Complications
B) Use of resources
i) Hospital stay
ii)No. of sessions
iii) Cost etc.
Need statistics
Review to confirm results
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.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-32 (2009)

Reviewer's report
Title:Montelukast in the treatment of duodenal eosinophilia in children with
dyspepsia: Effect on eosinophil density and activation in relation to
pharmacokinetics
Version: 1Date:27 January 2009
Reviewer: Stephen Attwood
Reviewer's report:
This study is well thought out and executed with a good protocol. The findings
are within expectations based on previous reports of the clinical efficacy of
Montelukast in diseases of excess esinophilic inflammation without demonstrable
changes in Eosinophil density or eosinophilic granulation activation.
The authors correctly identify (discussion page 16) that the methods of activation
of eosinophils and their degranulation are complex and the tests employed in this
study may be insensitive to detect a real effect.
It would be useful in future studies to consider the wider mast cell and eosinophil
activation pathway described by Blanchard et al and test for a wider range of
eosinophil related effects in order to look for the mechanism of clinical benefit of
montelukast. (Blanhard C, Wang N, Stringer KF et al Eotaxin-3 and a uniquely
conserved gene expression profile in eosinophilic esophagitis. J Clin Immunol
2006: 116: 536 – 47.
Suggested minor essential revisions
Abstract line 4: Please define patients as “Twenty four dyspeptic patients…”
In the previous study they found elimination half life of montelukast to be 1.8
hours. The used a dose of 10mg once daily in the current study. Would it be
worthwhile dosing the patients b.d (5mg b d) in order to maintain a more
continuous therapeutic effect? This might also have a more measurable effect on
eosinophil function or activation. Please comment
Methods Subjects paragraph 2 last line: 20 cell/hpf. Define hpf ( I assume = high
power field) and state the surface area that your pathologist considers is a high
power field. There is much variation in the size of high power fields and a
description of the precise surface are in square millimeters is required.
Discretionary revisions
Background paragraph 2 line 2 consider stating “..we found duodenal mucosal
eosinophilia in 71%.....”
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-9-32 (2009)

Reviewer's report
Title:Montelukast in the treatment of duodenal eosinophilia in children with
dyspepsia: Effect on eosinophil density and activation in relation to
pharmacokinetics
Version: 1Date:27 January 2009
Reviewer: jon A vanderhoof
Reviewer's report:
No revisions needed
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.
Review for 10.1186/1471-230X-9-32 (2009)

Reviewer's report
Title:Montelukast in the treatment of duodenal eosinophilia in children with
dyspepsia: Effect on eosinophil density and activation in relation to
pharmacokinetics
Version: 1Date:5 February 2009
Reviewer: Frantisek Kopriva
Reviewer's report:
The author must complete demograhpic patient data, history of atopy - family and
patiens, family history of dyspepsia, kind of cuisine ?
The method of morphologic evaluation eosinohpilic granules is not very precise.
The pharmakokinetic study of montelukast is innapropriate for evaluation clinical
response in pateints with dyspepsia. Leukotrienens are effector meidators of
neurogenic inflammation. The author must complete discussion in relationship
between eosinophils and mast cells, regulation of neurogenic inflammattion.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I have no interests
Review for 10.1186/1471-230X-9-32 (2009)

Reviewer's report
Title:Montelukast in the treatment of duodenal eosinophilia in children with
dyspepsia: Effect on eosinophil density and activation in relation to
pharmacokinetics
Version: 1Date:16 February 2009
Reviewer: G Riccioni
Reviewer's report:
1. Is the question posed by the authors well defined? The question is well
defined.
2. Are the methods appropriate and well described? The methods are
appropriate.
3. Are the data sound? Yes.
4. Does the manuscript adhere to the relevant standards for reporting and data
deposition? Yes.
5. Are the discussion and conclusions well balanced and adequately supported
by the data? The discussion may be improved on the basis of the recents
published results.
6. Are limitations of the work clearly stated? NO.
7. Do the authors clearly acknowledge any work upon which they are building,
both published and unpublished? Yes.
8. Do the title and abstract accurately convey what has been found? Yes.
9. Is the writing acceptable? The manuscript need to English revision.
Level of interest: An article of outstanding merit and interest 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' below.
Review for 10.1186/1471-230X-9-32 (2009)

Reviewer's report
Title:Montelukast in the treatment of duodenal eosinophilia in children with
dyspepsia: Effect on eosinophil density and activation in relation to
pharmacokinetics
Version: 2Date:14 April 2009
Reviewer: Frantisek Kopriva
Reviewer's report:
I think that authors accepted ned corrected my comments.
Level of interest: An article of limited interest
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-9-29 (2009)

Reviewer's report
Title:Outcomes and factors influencing the survival in cases with spontaneous
rupture of hepatocellular carcinoma: a multicenter study
Version: 2Date:2 January 2009
Reviewer: Spiros Delis
Reviewer's report:
This paper puts into context the previously exaggerated claims for spontaneous
rupture of HCC.
1. The manuscript and particular the discusion needs to be shortened
2.The manuscript i interesting due to the fairly large cohort of ruptured HCC
although the comparison groups are not similar regarding liver function.ConT
gr4oup seems to have less hepatic reserve compared to TAE group.
3. Although all patients died from re-rupture or liver failure in the ConT group
there is no reported effort for rescue TAE in this group of patients who developed
rebleeding.What was the reason?
4. There was also not reported any effort for liver resection in patients who
eventually survived by TAE .How many patients developed recurrence post TAE
and how they were treated during the follow up period before they finally died?
Do you use other strategies :such as RF ablation or repeated TAE