JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-9-58 (2009)

Reviewer's report
Title:The Pancreatic Zymogen Granule Membrane Protein, GP2, Binds
Escherichia coli Type 1 Fimbriae
Version: 1Date:7 April 2009
Reviewer: Michael Rindler
Reviewer's report:
This manuscript describes the binding of E. coli to GP2. GP2 is pancreatic
protein that is shed into the pancreatic juice. It is a relative of uromodulin, whose
ability to bind to fimbriated bacteria is well established. Using in vitro microplate
binding assays and recombinant GP2 and purified uromodulin, the binding of
fimbriated bacteria to GP2 is confirmed. Moreover GP2 is shown to bind to type I
fimbriae through mannose residues in the oligosaccharide side chains and it also
is capable of binding variants in fimbriae sequence that are normally poor
substrates for uromodulin. The authors speculate that GP2 may play a role in
protecting the pancreatic duct and bile duct from infection, similar to that thought
to be played by uromodulin in the urinary system.
The experiments are well conceived and performed. The conclusions are sound.
The findings are novel and I have no major criticisms.
There is one minor revision that I consider reasonable if not essential:
1. Concerning Figure 5, it should be possible to give a quantitative estimate as to
the relative affinity for each protein for the bacteria if not the absolute affinity.
Also, it seems the KB91 binding is substantially lower than Nu14 for GP2,
perhaps even in the same relative range as the difference for uromodulin.
Therefore, it appears that the overall affinity for binding the bacteria is much
higher, but the relative binding to the M1L and M1H is the same between the two
proteins.
There are a number of minor discretionary revisions that would improve the
manuscript:
1. In the Methods Reagents section, the procedures for purification of
recombinant GP2 should be explained at least briefly. The reader should not
have to refer to previous papers to understand if full length GP2 or secreted GP2
was used and what method was used to purify it. The purity of the recombinant
GP2 is a critically important issue and deserves a few sentences of explanation.
2. In the Results section, what is the explanation for the antibody blocking the
binding to fimbriae? The fimbriae should theoretically bind to oligosaccharides
even when the antibody is bound.
3. In Figure 5 it is difficult to see the data points for Nu14-THP in the graph. They
should be changed to circles or some other symbol.
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-9-58 (2009)

Reviewer's report
Title:The Pancreatic Zymogen Granule Membrane Protein, GP2, Binds
Escherichia coli Type 1 Fimbriae
Version: 3Date:3 June 2009
Reviewer: Carlos Balsalobre
Reviewer's report:
The amended version of the manuscript “The Pancreatic Zymogen Granule
Membrane Protein, GP2, Binds Escherichia coli Type 1 fimbriae” contains all
suggestions by this reviewer on the previous revision. Therefore I consider that
now is acceptable to be published in BMC Gastroenterology. There are still
typographical/language mistakes in the text that need to be corrected. Also some
sentences can be revised for better understanding of the readers:
- Last sentence of the Results section in the abstract, it is unclear.
- First sentence in Results …. Transfected with the gene…. I believe is most
appropriate mention the gene name …. Transfected with the XXX gene.
- Fig. 2B is not refereed on the text
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 ineterests
Review for 10.1186/1471-230X-9-58 (2009)

Reviewer's report
Title:The Pancreatic Zymogen Granule Membrane Protein, GP2, Binds
Escherichia coli Type 1 Fimbriae
Version: 3Date:8 June 2009
Reviewer: Luis Angel Fernández Herrero
Reviewer's report:
The revised manuscript has been improved to a reasonable extent, especially
because the wild speculations regarding the anti-infective role of GP2 in the gut,
which are now only mentioned in the Discussion. Binding of recombinant GP2 to
bacteria expressing type I fimbriae and FimH is established, although its
biological significant remains unsolved. A comparison of the binding to GP2 and
Uromodulin is now shown. A direct binding assay between purified FimH and
GP2 is still missing, but it may not be essential for this manuscript. Data are well
presented and the paper is brief and easy to read. Minor text corrections have
been made. The manuscript may be of sufficient quality to merit 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-9-59 (2009)

Reviewer's report
Title:Gastroesophageal reflux leads to esophageal cancer in a surgical model
with mice
Version: 1Date:7 August 2008
Reviewer: Takanori Hattori
Reviewer's report:
The authors deal with a mouse model of Barrett’s esophagus (BE) and
esophageal adenocarcinoma (EAC). They tried to establish this mouse model by
surgical procedure with esophago-gastroduodenal anastomosis (EGDA) on
wild-type, p53A135V transgenic, and INK4a/Arf+/- mice of A/J strain. However,
EGDA induced only esophageal squamous cell carcinoma (ESCC), but not BE
and EAC, in these mice.
The results are unexpectedly negative data. However, the study is well designed,
and the manuscript is well written. Moreover, the manuscript has some interests
about association between duodenal contents reflux and development of ESCC.
So, the manuscript should be accepted without any revisions.
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.
Review for 10.1186/1471-230X-9-59 (2009)

Reviewer's report
Title:Gastroesophageal reflux leads to esophageal cancer in a surgical model
with mice
Version: 1Date:6 November 2008
Reviewer: Glyn Jamieson
Reviewer's report:
The MS documents an interesting attempt to produce a mouse model of
adenocarcinoma of the esophagus via reflux.My major difficulty with reading the
paper was that the authors assume far too much knowledge on the part of the
reader. e.g.
1.What does the symbol -/- mean?
2.Is heterozygous knockout of INK4a/Arf the same thing as hypermethylation of
p14Arf and p16 INK4a? I think it needs to be at least stated otherwise the reader
is left wondering why this knockout was chosen.
3.Why was the mutant trasgene model chosen?
4.Why was this omeprazole dose chosen?And why was there no omeprazole
alone group?
5.Were the surgical procedures undertaken using magnification? How can you
be sure that the mucus glands wer e not just part of the duodenum which had
been hitched in during the anastomosis-particularly a problem using the Swiss
roll technique.
Other questions I have are;
1.There doesnt appear to be any pattern to the mice numbers chosen.The
numbers were 49, 52,36,42,24,5,36,30,26 and then 10 and10 for the
controls.Why were these numbers chosen?And there is no explanation given as
to why three of the groups had male and female mice and the other three had
only male mice.
2.Presumably there were good reasons for giving iron at the timings
chosen.These need to be explained.To see the effect of the iron each of the
groups needed a control group where iron wasnt given .
And a comment.I will never understand why authors seem to go out of their way
to make their paper hard to read by using unnecessary abbreviations.In this
paper I would accept only GERD .There is no more justification for contracting
esophageal adenocarcinoma to EAC than ,for instance contracting iron
supplementation to IS or poly clonal antibody to PCA.It is only in the
authors'interest that I make the comment since it will make the paper easier to
read.
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 thay I have no competing interests
Review for 10.1186/1471-230X-9-59 (2009)

Reviewer's report
Title:Gastroesophageal reflux leads to esophageal cancer in a surgical model
with mice
Version: 2Date:12 December 2008
Reviewer: Glyn Jamieson
Reviewer's report:
I am afraid that in a scientific study to be told that" the numbers in each group
were not in any fixed pattern "is to state that the design of the study was
flawed.This lays the authors open to the criticism that numbers were used until
the investigators obtained the results that they wanted to see.
The numbers required should always be determined in advance (using statistical
power calculations) so that the minimum number of animals is used to answer
the hypothesis posed.This is the only ethical way we can justify using animals for
scientific research.
Level of interest: An article of insufficient interest to warrant publication in a
scientific/medical journal
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
no competing interests
Review for 10.1186/1471-230X-9-57 (2009)

Reviewer's report
Title:Symptoms and signs in latent celiac disease - a validation study
Version: 1Date:5 May 2009
Reviewer: Vincenzo Villanacci
Reviewer's report:
The paper is well written with useful notices in the field of diagnosis and
treatment of coeliac disease. I suggest to accept the paper.
I ask to the authors only a specification about the number of intraepithelial
lymphocytes because at moment the normal value is 25-30 IEL for 100 epithelial
cells and in the classification of Marsh-Oberhuber was used the value 0f 40/100
epithelial cells. It is important in the text of the paper this specification.In the
bibliography I suggest to enclose two papers on the argument.
Hayat M, Cairns A, Dixon MF, O'Mahony S.
Quantitation of intraepithelial lymphocytes in human duodenum: what is normal?
J Clin Pathol. 2002 May;55(5):393-4.
Veress B, Franzen L, Bodin L, Borch K.
Duodenal Intraepithelial Lymphocyte Count Revisited
Scand J Gastroenterol 2004 Feb;39(2):138-44.
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-9-57 (2009)

Reviewer's report
Title:Symptoms and signs in individuals with serology positive for celiac disease
but normal mucosa
Version: 2Date:2 July 2009
Reviewer: Kamran Rostami
Reviewer's report:
I am very glad with the modifications and adjustment and would be more than
happy to support the publication of this paper in BMC Gastroenterology!
Kamran Rostami
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
Kamran Rostami
Review for 10.1186/1471-230X-9-56 (2009)

Reviewer's report
Title:Visceral Obesity and the Risk of Barrett's Esophagus in Japanese Patients
with Non-alcoholic Fatty Liver Disease
Version: 1Date:3 May 2009
Reviewer: Yoshihisa URITA
Reviewer's report:
Dear Dr. Akiyama,
Your manuscript entitled “Visceral obesity and the risk of Barrett’s esophagus in
Japanese patients with non-alcoholic liver disease” has been reviewed. The
authors conclude that the existence of a significant association between visceral
obesity, as measured on abdominal CT images, and the risk of BE in a Japanese
population with NAFLD. However, I don not accept that their conclusions are
valid although this manuscript provides some interesting results. This paper has
some problems revised.
1. 172 consecutive NAFLD patients (86 men and 86 women) who underwent
both endoscopy and abdominal CT were recruited in this study. BMI ranged from
16.7 to 43.6. A patient with a BMI of 16.7 is considered as skinny, and might
have a different mechanism of developing fatty liver disease from an obese
patient. The author should analyze after separating skinny patients from obese
ones.
2. The author should describe the patients taking drugs that have the possibility
of modification to LES pressure as a consequence of medication such as Ca
channel blockers. Patients with metabolic syndrome are frequently suffering from
hypertension.
3. Why was NAFLD diagnosed according to the ultrasonographic findings? It is
because all patients underwent abdominal CT. We sometimes experienced the
NAFLD patient with different diagnosis by the method using US and CT. I think
that abdominal CT is superior to the diagnostic ability compared to US.
4. On the result section, it was described that VAT (OR, 1.007; 95% CI,
1.000-1.015) showed an independently significant association with the risk of BE.
Is this a true? When OR was 1.007, this value may not be considered as
statistically significant.
5. Do the author think whether the same conclusions may be drawn after patients
with ALD are included? Or, is a significant association between visceral obesity
and the risk of BE limited to NAFLD? The author should describe this point on
the Discussion section.
I believe that you can modify your paper by considering the above-mentioned
comments to make this paper into better form. Major Compulsory Revisions are
required.
Yours sincerely,
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.
Review for 10.1186/1471-230X-9-56 (2009)

Reviewer's report
Title:Visceral Obesity and the Risk of Barrett's Esophagus in Japanese Patients
with Non-alcoholic Fatty Liver Disease
Version: 1Date:5 May 2009
Reviewer: Elfriede Bollschweiler
Reviewer's report:
Akiyama and colleagues described in a retrospective study the correlation of BMI
and visceral obesity with the existence of Barrett Mucosa. They measured the
visceral obesity with the help of CT. I think that this paper is of great interst by
several points:
1. Barrett esophagus is an actual topic because of the risk for adenocarcinoma of
the esophagus.
2. In Japan the incidence of AC of the esophgus as well as gastroesophgeal
reflux is rare.
3. In this study the authors analysed patients with fatty liver disease.
This is a group with a higher prevalence of visceral obesity. And they found a
high rate of Barrett mucosa in this group.
4. The method for measuring visceral obesity is adequate.
The manuscript is well written, the statistical methods are adequate.
In my opinion the paper should be published in the present form.
Review for 10.1186/1471-230X-9-56 (2009)

Reviewer's report
Title:Visceral Obesity and the Risk of Barrett's Esophagus in Japanese Patients
with Non-alcoholic Fatty Liver Disease
Version: 1Date:9 May 2009
Reviewer: Piers Gatenby
Reviewer's report:
This is a well-written and interesting study.
I have only recommendations for minor revisions.
Minor Essential Revisions:
Cohort:
Could the authors explain a little more about the study cohort, including what
other investigations they are undertaking in examining for associations between
obesity patterns and diseases?
Results
Remove word “about” at beginning of 3rd sentence of first paragraph as this is an
exact calculation.
40.1% refers to the whole cohort, not the group with Barrett’s – this should be
clarified.
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-9-56 (2009)

Reviewer's report
Title:Visceral Obesity and the Risk of Barrett's Esophagus in Japanese Patients
with Non-alcoholic Fatty Liver Disease
Version: 2Date:14 July 2009
Reviewer: Yoshihisa URITA
Reviewer's report:
My suggestion has been accepted in the revised manuscript.
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-9-55 (2009)

Reviewer's report
Title:Interrelationship between TP53 gene deletion, protein expression and
chromosome 17 aneusomy in gastric adenocarcinoma
Version: 1Date:11 February 2009
Reviewer: Haruhiko Sugimura
Reviewer's report:
This is a small scale, confirmative work. The data is concise and easily
understand.
Many LOH papers adopt the famous Knudson's scheme having two
chromosomal status changed into single allele deletion in retinoblastoma.
Actually, as the authors and the others believe, many tumors has 3 and more
chromosomes in each. One question may be raised about expression level and
polysomy pattern. How about relative loss (like in the table of Kobayashi M
paper(ref20)) in terms to expression level?
1. Figures are clear, but you have to show intestinal and diffuse type
representative cases2. with p53 immunostaining and FISH.
2. In diffuse type, definite LOH (not relative one) of p53 seems to be rampant,
which is consistent with the early stage diffuse type cancer often near diploid
(cite hereditary diffuse gastric cancer dormant stage), thus the inconsistency with
ref 23 would not be necessarily due to geographical difference, but to difference
in stage when observation was done.
3. Percentage of normal karyotype in tumors are high. Is it consistent with clonal
expansion of tumor cells with abnormal chromosomal status?
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-9-55 (2009)

Reviewer's report
Title:Interrelationship between TP53 gene deletion, protein expression and
chromosome 17 aneusomy in gastric adenocarcinoma
Version: 1Date:6 April 2009
Reviewer: ANNA D PANANI
Reviewer's report:
Comments
The authors investigated by FISH technique numerical aberrations of
chromosome 17 and TP53 gene deletion in 20 cases of gastric adenocarcinoma.
They also evaluated the p53 expression in these samples. Results were
correlated with clinicopathological features. Aneusomy 17 was found in 85% of
the cases, while deletion of TP53 was found in all cases. Immunoreactivity of p53
was found only in 8 intestinal type gastric cancer cases.
The study is well organized and the methods are appropriate and well described.
Although, the number of cases studied is small (12 cases of intestinal type and 6
cases of diffuse type gastric cancer) the discussion and conclusions are
adequately supported by the data.
Discretionary revisions:In References a recent review article “ Cytogenetic and
molecular aspects of gastric cancer: clinical implications” (Cancer Letters 266,
99, 2008) could be added.
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 interest.
Review for 10.1186/1471-230X-9-55 (2009)

Reviewer's report
Title:Interrelationship between TP53 gene deletion, protein expression and
chromosome 17 aneusomy in gastric adenocarcinoma
Version: 1Date:7 April 2009
Reviewer: Tamotsu Sugai
Reviewer's report:
The author indicates that there are chr17 and TP53 copy number alterations in
gastric cancers. Although this manuscript is generally well written, several points
regarding the work are listed below:
1. The author analyzed 20 intestinal- and diffuse-type gastric cancers for
chromosome 17p and TP53 copy number alterations. However, the number of
tumor samples examined is too small to determine the role of 17p and TP53 copy
number alterations in gastric carcinogenesis. To examine the role of 17p and
TP53 copy number alterations in gastric carcinogenesis, the author should
increase the number of tumor samples.
2. Although the manuscript has some novel findings, in its present form the
author has not provided new findings about gastric carcinogenesis.
3. The author suggests that deletion of TP53 and chromosome 17 aneusomy are
common events in gastric cancer and that p53 mutation may be implicated in the
distinct carcinogenic process of diffuse- and intestinal-type cancers. However,
contrasting data were given. The author should discuss in the text the roles of
TP53 deletion, chromosome 17 aneusomy, and p53 mutation with regard to
intestinal- and diffuse-type cancers.
4. This study could not clarify the role of the above-mentioned alterations in the
early development of gastric cancers. The author should discuss this point in the
text.
5. In the Materials and Methods section the author should describe in detail the
FISH method that was used.
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' below.
Review for 10.1186/1471-230X-9-55 (2009)

Reviewer's report
Title:Interrelationship between TP53 gene deletion, protein expression and
chromosome 17 aneusomy in gastric adenocarcinoma
Version: 2Date:19 May 2009
Reviewer: Haruhiko Sugimura
Reviewer's report:
The revision is well done and convincing.
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-9-54 (2009)

Reviewer's report
Title:Quality of life following liver transplantation: a comparative study between
Familial Amyloid Neuropathy and liver disease patients
Version: 1Date:28 April 2009
Reviewer: Naoki Kawagishi
Reviewer's report:
This manuscript clarified the QOL of the FAP patients after liver transplantation.
But there are still some refinements needed in this manuscript.
Major
1, Authors used the DIFQL and QLBT, but these are not universal measurement.
They should explain the precise details and why this measurement is suitable for
this analysis. Otherwise the concept of this manuscript is not clear.
2, The type of complications should be showed in table, because these things
affect the QOL after liver transplantation seriously. The severity of complication is
also important factor.
Minor
1, Authors inserted the (TABLE 1, 2,3) in the text, but this kind of things should
be avoided.
2, I can not understand the meanings of subgroups(N=131) in Table 1.
3, In table 2, what the “z” means? Please clarify.
4, Why authors should have performed liver transplantations for the patients of
Child Pugh A except FAP. Please show the primary disease of those recipients.
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' below.
Review for 10.1186/1471-230X-9-54 (2009)

Reviewer's report
Title:Quality of life following liver transplantation: a comparative study between
Familial Amyloid Neuropathy and liver disease patients
Version: 1Date:9 May 2009
Reviewer: Raaj Praseedom
Reviewer's report:
Major essential revisions
1) Please indicate the selection criteria for the study group. Are these 62 patients
consecutive liver transplant recipients? If not, what are the exclusion criteria?
Give details on the patients excluded from the study during the study period with
reasons for exclusion.
2) What was the QOL in these 2 groups compared to the general Portuguese
population? Were they significantly different pre and post operatively?
3) Did age, sex, retransplantation, complications, repeat surgery etc have an
effect on the QOL?
4) Essential surgical details of the recipients are missing e.g. re-laparotomy,
surgical complications, hospital stay, type of donor (?living donor) etc
Minor essential revisions
1) Please make English language corrections!
2) The 'Background' section has numerous mistakes e.g. repeat usage of month,
paranthesis on 8TTR, spelling of methionine, choroid plexus and not choroids
plexus,
3) 'QOL evaluation' section has a few mistakes e.g. commas after each
subscales on SF36 missing, change 'witch' to which please!
4) Change 'an hepatologist' to a hepatologist.
5) Some of the references in the text are in superscripts and some in
paranthesis. Change to uniform requirements for the journal.
6) Sales-Luis e col [14] - what is e col? is it et al? Why is the text here in a
different colour?
Discretionary revisions
1) QOL is often subjective especially the difference in QOL as perceived by an
individual. This is difficult to estimate and a scientific way of doing so is to use
some thing like a Ferrans & Powar questionnaire which looks at the difference in
QOL as perceived by the patient. For e.g. some patients may have an
improvement in their SF36 scores, but they do not necessarily perceive an
improvement in their QOL and vice versa. Consider acknowledging the use of a
different dedicated QOL instrument in these patients (Desai et al Liver Transpl
2008;14(10):1473-9 and the editorial)
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-9-53 (2009)

Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is delayed
by phosphatidylcholine in intestinal epithelial cells
Version: 3Date:24 October 2008
Reviewer: Jan Wehkamp
Reviewer's report:
The data by Treede at al. are sound, fit well to already published data and the
experiments seem well done. I only have some minor comments which might add
the quality of paper discusssion.
Figures: in my view, the figures would benefit from the inclusion of some
statistical analysis- even though the differences seem very clear.
Introduction: It is possible - or even likely- that the immune response is
adaequate and secondary due to the entry of bacteria. The authors should make
their first sentnce statement more carefull in less exclusive.
Discussion and introduction: NFkB also regulates many protective factors
including inducible beta defensins (e.g. induction of beta defensins by probiotic
bacteria, Infection and Immunity 2004). Eptithelial knock out of NFkB leads to
intestinal inflammation at least partyl associated with a lack of beta defensins.
Both aspects should be added in order to avoid a too simplistic view of nFkB and
its role in inflammatory regulation.
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-9-53 (2009)

Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is reduced
by phosphatidylcholine in intestinal epithelial cells
Version: 4Date:9 March 2009
Reviewer: Alexandr Parlesak
Reviewer's report:
Regarding previous objections on their manuscript on the mechanism leading to
down-regulation of TNF-#-induced inflammation in Caco-2 cells by
phosphatidylcholine (PC), the authors have improved the txt considerably. I have
only a few minor essential revisions to suggest:
Minor essential revisions
1) The Abstract seems quite long to me – no limits from the editorial office?
2) In the Results part of the Abstract: Replace ‘monocyte chemoattractant
proteins’ by ‘monocyte chemoattractant protein’; besides that, it should either be
stated that SN 50 is a NFkB inhibitor or ‘SN 50’ should be omitted in the Abstract.
3) The last sentence in the Conlusion part of the Abstract is misleading; it can be
read also as TNF-# would trigger signaling from both the apical and the
basolateral side, which is evidently not true.
4) In the Background and the Discussion, the expression ‘in this respect’ is used.
I suggest to replace it with ‘with respect to this’.
5) In the Methods, part ‘Lipids and reagents, it should be stated that SN 50 is a
NFkB inhibitor – the sense of the experiment is hard to understand if this
information is not given.
6) In the Methods, locations for RnD systems, RAS, and Startagene should be
given as well. Provide used concentration of cells in the Flow cytometry section
and reveal the source of radiolabelled PC. What is a’postnuclear supernatant?
7) In the Results section, part ‘Expression of pro-inflammatory …’, the authors
state in the first paragraph that TNF-#-mRNA expression was not enhanced by
TNF-# treatment. In the second paragraph, they state the opposite – clear this
contradiction.
8) For Figure 7, a higher resolution should be provided.
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-9-53 (2009)

Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is reduced
by phosphatidylcholine in intestinal epithelial cells
Version: 4Date:11 March 2009
Reviewer: Eva Rath
Reviewer's report:
Too few new data to publish:
Figure 1 A: effect shown in a different readout
see article * Figure 5C
Figure 1B: similar data already published;
see article * Figure 5D: (difference: PC 18:2)
Figure 2: time course of 1B, ok
Figure 3: similar data already published;
see article * Table1: (4%<->95%?)
Figure 4: similar data already published;
see article * Figure 6A: (new: MMP-1, t=240min)
Figure 5: ok; MCP-1: TNF+SN50 higher induction than TNF after 120min?
ICAM-1: TNF+SN50 and TNF: similar induction after 120min?
Figure 6: PC do not inhibit TNF binding to its receptor; ok
Figure 7: Lipid raft association:
“PC and LPC induced also an increased DRM association for the raft marker
proteins Yes and Flotillin.1 (data not shown) that served as controls” -> not TNF
Receptor specific effect
Figure 8: apical/basolateral TNF stimulation;
known effect in polarized cells
Figure 9: PC effective for apical & basolateral side; ok
*Anti-inflammatory effects of phosphatidylcholine.
Treede I, Braun A, Sparla R, Kühnel M, Giese T, Turner JR, Anes E, Kulaksiz H,
Füllekrug J, Stremmel W, Griffiths G, Ehehalt R.
J Biol Chem. 2007 Sep 14;282(37):27155-64. Epub 2007 Jul 18.
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-9-52 (2009)

Reviewer's report
Title:Early effects of oral administration of lafutidine with mosapride compared
with lafutidine alone on intragastric pH values
Version: 1Date:17 March 2009
Reviewer: Spiros Ladas
Reviewer's report:
In this study Iida et al compare the effect of the co-administration of an H-2
receptor antagonist (lafutidine) and a prokinetic (mosapride) versus the
administration of the H-2 receptor antagonist alone, on the intragastric pH during
the immediate post-administration period. The hypothesis to test is that the
co-administration of the prokinetic would accelerate the absorption of the H-2
antagonist by accelerating gastric emptying resulting in a more rapid and
effective on-demand therapy for GERD.
Major Compulsory Revisions
In the introduction (line 9) the authors state that their study was aiming to
examine whether H2RA + mosapride could more rapidly increase intragastric pH.
This is repeated in the Discussion (page 9, lines 10 and 15-16). However, they
have not measured the time elapsed since the administration of the drug(s) for
intragastric pH to increase above a certain pH, e.g. 4, 5 or 6.
Minor Essential Revisions
1. The authors comment that the combined administration of lafutidine and
mosapride could be an effective on-demand therapy for GERD. However, they
have studied healthy volunteers and not GERD patients requiring on-demand
therapy. They should, therefore, comment on this in the discussion section.
2. In the Background page 4) the authors comment about gastric ulcer
haemorrhage and gastric pH. This is not relevant with study and should be
omitted (lines 1-4)
3. The authors may wish to refer and comment on a recently published study on
the same topic (Dig Dis Sci. 2008;53:3128-32)
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, 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-9-52 (2009)

Reviewer's report
Title:Early effects of oral administration of lafutidine with mosapride compared
with lafutidine alone on intragastric pH values
Version: 1Date:24 March 2009
Reviewer: Carmelo Scarpignato
Reviewer's report:
This is a straightforward paper dealing with a pharmacodynamic interaction
between a prokinetic compound (mosapride) and a novel H2-receptor antagonist
(H2RA), namely lafutidine.
Despite all the intrinsic limitations, there is still a place for H2RAs in the era of
PPIs. Besides controlling NAB (i.e. Nocturnal Acid Breakthrough), often observed
even with twice daily PPIs, H2RAs (especially soluble or OTC formulations) will
become the “antacids of the third millennium” and will be particularly useful for
on-demand symptom relief. The onset of the antisecretory will then be
particularly important. In this connection, this work is a welcome one since it does
give an additional rationale for adding a prokinetic agent to an antisecretory
compound. Indeed, in GERD this combination (usually with a PPI) has been
adopted to increase gastric emptying rate (often delayed in a significant
proportion of patients), thus reducing in that way the amount of gastric contenta
available for reflux. Yet, another good reason could be to speed up the intestinal
absorption of the antisecretory compound (be it a PPI or an H2RA) and achieve a
quicker increase of intragastric pH, with consequent quicker symptom control.
This pharmacodynamic study clearly shows that this is the case. The paper is
well written, the methodology is simple and correct, data are presented and
discussed clearly.
It is not stated whether the subjects under investigation were fed or (as I guess)
fasted. A similar experiment in fed subjects, measuring also post-prandial
intra-esophageal pH, could be particularly useful to evaluate the effect of this
drug combination on esophageal exposure to acid.
In addition, I am sure blood samples have been collected during the study. If this
is the case, the investigators should measure lafutidine pharmacokinetics and
quantitate the relevant PK parameters (Cmax, Tmax, AUC, etc) to give the
readers a better insight into the clinical relevance of this drug combination.
The authors should also discuss the potential clinical utility of a fixed
mosapride-lafutidine combination, where a specifically developed formulation
could assure a sequential release of the different compounds.
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
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-9-52 (2009)

Reviewer's report
Title:Early effects of oral administration of lafutidine with mosapride compared
with lafutidine alone on intragastric pH values
Version: 2Date:2 June 2009
Reviewer: Spiros Ladas
Reviewer's report:
Minor essential revisions
The author nshould state in the abstract and the backgroung what are Lafutidine
(H2RA) and Mosapride (gastrokinetic)
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-9-52 (2009)

Reviewer's report
Title:Early effects of oral administration of lafutidine with mosapride compared
with lafutidine alone on intragastric pH values
Version: 2Date:11 June 2009
Reviewer: Carmelo Scarpignato
Reviewer's report:
The paper is now acceptable, since the Authors have taken all the comments into
consideration in the revised version.
Review for 10.1186/1471-230X-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 1Date:29 October 2008
Reviewer: Haruhiko Sugimura
Reviewer's report:
major:
It is not clear to calculate OR for the subpopulation of severe gastric atrophy and
Hp infected severe gastric atrophy. Please state clearly what this subpopulation
represent?
minor
A seronegative, but sever gastric atrophic population were added in table 4b and
it generated the significant difference. What explains the seronegative gastric
atrophy? Is it the same pathway in seropositive atrophy?
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. HS
Review for 10.1186/1471-230X-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 3Date:29 December 2008
Reviewer: Haruhiko Sugimura
Reviewer's report:
The responses well explains the assumptions they took for the interpretation of
their data.
They bluntly state, all the Japanese gastric cancer is related to HP infection, and
HP seronegative atrophy is also a consequence of burned out infection. The
hypothesis require validation. There are may be quite a few factors including
genetic ones to make the individual stomach for stable HP colonization, given
endemic access occasions to HP for every Japanese granted (Short mucin 1
alleles are associated with low virulent H pylori strains infection. Peleteiro B,
Lunet N, Santos-Silva F, David L, Figueiredo C, Barros H. World J Gastroenterol.
2007 Mar 28;13(12):1885-6, Natural antibiotic function of a human gastric mucin
against Helicobacter pylori infection. Kawakubo M, Ito Y, Okimura Y, Kobayashi
M, Sakura K, Kasama S, Fukuda MN, Fukuda M, Katsuyama T, Nakayama J.
Science. 2004 Aug 13;305(5686):1003-6.) and they may confound or cancel the
effect of this polymorphism, if there are any.
Their hypothesis and its limitation should be included.
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-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 3Date:12 January 2009
Reviewer: charles S rabkin
Reviewer's report:
The revised manuscript has not answered our original criticism. The Abstract still
states, "Distribution of the genotype in patients with gastric cancer was similar to
that for those with gastric atrophy." This comparison is arbitrary and misleading,
since atrophy (i.e., mild+severe) is not significantly different from no atrophy. The
non-significant comparison of gastric cancer to no atrophy and the increased
odds ratio for gastric cancer compared to severe atrophy support a very different
interpretation. At the very least, the Abstract should include the authors' response
statement that "...those with the A/A genotype of PTPN11 rs2301756
polymorphism are at lower risk of severe gastric atrophy, but not associated with
the decreased risk of gastric cancer."
Furthermore, we support Dr. Ghoshal's comment #7 requesting a satisfactory
explanation of these paradoxical observations. The revised manuscript has not
yet adequately addressed our common concern.
/s/ Charles S Rabkin MD and Gwen Murphy PhD
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
We declare that we have no competing interests.
Review for 10.1186/1471-230X-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 3Date:15 January 2009
Reviewer: Uday Ghoshal
Reviewer's report:
I am satisfied with revision. Though some issues still remains, authors did clearly
mention that due to lack of data, the present paper can not resolve all these
issues. Further studies are needed to resolve these issues.
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.
Review for 10.1186/1471-230X-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 4Date:6 April 2009
Reviewer: charles S rabkin
Reviewer's report:
Major suggested revision:
Change the comparison group for the last paragraph of Results/Table 5 from
gastric atrophy (n=536) to HP-infected without atrophy (n=686).
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-9-51 (2009)

Reviewer's report
Title:Associations of a PTPN11 G/A polymorphism at intron 3 with Helicobactor
pylori seropositivity, gastric atrophy and gastric cancer in Japanese
Version: 5Date:8 June 2009
Reviewer: charles S rabkin
Reviewer's report:
The authors have now included the alternative comparison of PTPN11
polymorphism carriers to HP+ subjects without atrophy, as suggested in our
previous reviews.
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:
We declare that we have no competing interests.
Reviewed with Dr. Gwen Murphy.
Review for 10.1186/1471-230X-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 1Date:16 December 2008
Reviewer: Miguel A. Serra Desfilis
Reviewer's report:
Major compulsory revisions: It is important to know the status of cirrhosis when
the GEC was performed in spite of the value of the test itself.
Minor compulsory revisions: In material and methods it is important to give more
information about the statistical methods. THe results needs more information in
tables specially the Cox regression
Discretionry revisions: The etiology of cirrhosis could be important and the
comparison with classical methods Child Pugh.
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-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 1Date:17 December 2008
Reviewer: Teh-Ia Huo
Reviewer's report:
The authors investigated 781 cirrhotic patients undergoing GEC test and their
long-term outcome. They found that GEC is a useful prognostic test for cirrhotic
patients. The idea of using GEC to evaluate liver functions is not new. Besides,
there are some flaws in this study that may deserve the authors’ attention.
1. The methodology of the GEC test should be given in detail. References 14, 16
and 17 were published during 1964-1977, which has been quite a while from
now.
2. The diagnostic criteria of cirrhosis were not given. Different hospitals may use
different criteria that may result in an inhomogeneous group of patients. How
many of them actually had a histological diagnosis of cirrhosis?
3. The risk of mortality in cirrhotic patients is best expressed as the risk ratio per
unit increase of the GEC mmol/min after adjusting for other confounding factors
in the Cox proportional hazard model.
4. More data should be reported in the Results section. Survival curves using
different cutoffs of GEC should be plotted against time to show how GEC level
may be associated with the short and long-term survival. In the last sentence of
the Results, the authors stated that “… … and was also present among the 29%
of patients with comorbidity”. What are other comorbidities? And how did these
comorbidities affect the outcome in this study?
5. It is interesting to know whether other liver functional assay, such as ICG test,
was done for the study patients? Which is more accurate?
6. There is not much new information in the Discussion.
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, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests.