JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-11-10 (2011)

Reviewer's report
Title:The overexpression of Sterol Carrier Protein 2 gene in patients of
hereditary cholesterol gallstones
Version: 6Date:5 October 2010
Reviewer: Silvana Zanlungo
Reviewer's report:
This is a good descriptive study in which authors analyze the hepatic expression
levels of SCP2 in hereditary, non-hereditary and non-cholesterol gallstone
patients. The most important contribution of this work is undoubtedly the analysis
of human samples. The manuscript is the continuation of previous studies
looking to analyze whether the expression of SCP2 may correlate with
cholesterol biliary lithiasis in humans. The methodology for measuring SCP2
mRNA levels should be improved. The presentation of the manuscript could be
improved. The English of the manuscript requires modifications. Figures can be
improved to make them more informative and friendly.
Major compulsory revisions
I suggest changing your method for analyzing mRNA levels of SCP2 for a more
quantitative method: semi quantitative methods that include competimer
technology or Real Time PCR. This is a crucial point for this manuscript and is
needed for make it stronger.
Minor Essential Revisions
Title
Please check if with or of is used for “patients of/with hereditary cholesterol
gallstones”
Abstract
Improve English.
Introduction
Improve English. Change and update references for cholesterol gallstones,
authors should use reviews instead of SCP2 specific references (for example for
references 1 and 2).
Results
Improve English. For example, what does it mean “To explore the potential
mechanisms of SCP2 gene”?
Figure 1: Improve English of the legend. Include liver or hepatic expression.
Clearly indicate in the figure the significant differences. “SCP2 mRNA” in the y
axis should be “SCP2 mRNA relative levels (SCP2/GAPDH)”
Figure 2: Include liver or hepatic expression in the legend. Is this a representative
Western blot? Were all samples analyzed by Western blot?
Figure 3: Y axis: bile lipid concentrations; x axis; Control instead of cotrol
Discussion
Improve English and references cited. The paragraph that proposes different
mechanisms for SCP2-mediated cholesterol increase in bile and lithogenicity is
not well written and referenced.
Level of interest: An article of importance in its field
Quality of written English: Not suitable for publication unless extensively edited
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-11-10 (2011)

Reviewer's report
Title:Overexpression of Sterol Carrier Protein 2 in patients with hereditary
cholesterol gallstones
Version: 7Date:17 December 2010
Reviewer: Silvana Zanlungo
Reviewer's report:
The manuscript has been improved and the authors have responded to most
questions from the reviewers.
English needs some language corrections before being published.
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-11-10 (2011)

Reviewer's report
Title:Overexpression of Sterol Carrier Protein 2 in patients with hereditary
cholesterol gallstones
Version: 7Date:28 December 2010
Reviewer: Michael Fuchs
Reviewer's report:
The revised version of this manuscript has addressed the reviewer comments
with satisfaction. The reference list should be revised to eliminate duplicate
references (e.g. ref. 11 and ref. 22 are identical).
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-11-9 (2011)

Reviewer's report
Title:Dietary intakes in subjects with irritable bowel syndrome
Version: 1Date:13 July 2010
Reviewer: Per G Farup
Reviewer's report:
The paper describes the diet in subjects with IBS. It is correct that relatively few
studies have undertaken dietary assessments in this group of patients, at least
concerning micronutrients. The paper is well written and easy to read.
Some revisions that should be clarified:
The introduction is long and detailed, the information given is well known for
readers of gastroenterological journals. The introduction would have been more
suitable in a nutritional journal read by nutritionists. I recommend a shortening.
The methods are well described.
The “results” section needs a revision. The text uses the words: similar, below,
exceed, far exceed, higher, lower etc. I want to know if the differences were
statistically significant. In more detail – on page 6: Only male subjects showed a
significant difference in BMI across IBS subtypes (p=0.036, data not shown). I
find the data in table 1.
Table 1 is ok. Table 2 is a very detailed description of the dietary intake divided
between sex and IBS-subgroups. It might be ok, but if possible, try to simplify it.
And make it clear also in the legend to the table that there were no statistically
significant differences between the groups.
Figure 1 is not one figure but 16, and figure 2 is 10 figures. I do not recommend
publication of these figures. Except for the reference values (RNI and NDNS), the
results in the figures are also given in table 2, the only difference is that in table 2
the results are given as mean with SD and in the figures as median with
percentiles. If the authors want to refer to RNI and NDNS for energy, macro- and
micronutrients, fruit and vegetables dived into groups for sex and IBS subtypes,
please find another way to do it – probably a table. More important for me is to
know if the intake is statistically significantly above or below the RNI and NDNS.
The most important information is probably the proportion of subjects below the
recommended limits and therefore in danger of deficiency disorders, which is not
mentioned at all.
I also lack information about the relation between the diet and comorbidity (e.g.
psychiatric disorders), food intolerance, degree of symptoms, ethnicity, etc. The
paper mentions trigger foods, have trigger food (like wheat and lactose) been
registered and how did trigger food influence the diet? I hope/expect that some of
this information could be added.
Figure 2 is not mentioned in the text, and abbreviations (like RNI) should be
explained before taken into use.
The discussion has to be revised based on the new way of presenting the
results.
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-11-9 (2011)

Reviewer's report
Title:Dietary intakes in subjects with irritable bowel syndrome
Version: 1Date:12 October 2010
Reviewer: Stine Störsrud
Reviewer's report:
Major Compulsory Revisions
1. What are the main aim(s)? To analyse for differences between subgrous and
gender or to compare to the general population and recommendations?
(methods vs results).
2. The aims of the study were to compare IBS patients to dietary recommended
values and population intakes, as well as assessing by gender and IBS subtype.
There are however no hypothesis or discussion about why there should be
differences in the dietary intake between gender or IBS subtype.
3. More information about the NDNS, i.e. method used for measuring dietary
intake, basic demographics.
4. Were the controls (NDNS) matched for gender, age, BMI...?
5. BMI of the IBS subjects compared to the healthy population (NDNS)?
6. The FFQ used (before modification) was found to give higher values for most
nutrients than other methods (according to ref 17). Could this explain the results?
7. No statistics used when comparing IBS subjects and NDNS as well as
recommended values.
8. A very few number of men, especially when presented by subtype (type A n=7,
type C n=5, type D n=11), is it meaningful dividing only 23 male subjects into
subtypes? Statistical analysis in 5-11 subjects?
9. No p-values in tables, only a few in the text (BMI in male subtypes).
10. Describe the results from previously done studies on dietary intake in IBS
subjects using 3-day dietary record or dietary recall. Did the FFQ method present
other/devian results?
11. Exclusion criteria: taking medication for their IBS. Any medications? For how
long? Does this means that the IBS subjects were relatively healthy IBS
patients? Could this explain the results?
Minor Essential Revisions
1. At page 7 and 8 the authors speculate about the higher intake of selected
micronutrients in the IBS subjects compared to reference nutrient intakes and
NDNS. This is not results, should be a part of discussion.
2. Page 8: Presentation of the intake of fruit and vegetables and alcohol - why
revise this when it was not part of the aim(s) of the study and when suggesting
that the high intake in the IBS subjects was a consequence of over-reporting.
Alcohol could/should be presented as macronutrients.
3. The authors describe in the background about IBS-subjects to restrict their
food intake of eliminate provocative dietary agents as lactose or wheat.
References or speculations?
Discretionary Revisions
1. Explain o and * in figures.
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-11-9 (2011)

Reviewer's report
Title:Dietary intakes in people with irritable bowel syndrome
Version: 2Date:7 December 2010
Reviewer: Per G Farup
Reviewer's report:
The revision has markedly improved the paper, but I still recommend some minor
revisions and clarifications.
It is my impression that the authors have limited experience with scientific writing,
and the paper could easily be improved with some assistance. Beyond that, the
language is of course good. I propose the following minor revisions.
1. The participants are referred to as “people with IBS”, “IBS sufferers”, “IBS
patients”, “IBS participants” and perhaps more. Please be consistent and correct.
You do not know if they suffer (but they have symptoms), and they are not
patients (they are recruited via posters etc.). I also strongly dislike “IBS subjects”.
I have seen hundreds of these people and have never seen an “IBS subject” or
“IBS patient”, but hundreds of subjects and patients with IBS (we have to refer to
people with respect!) I prefer “subjects with IBS” since they are recruited from the
general population after advertising.
2. The “Result” contains a lot of double information. The text refers to the table,
and when I have studied the table and return to the text, I find exactly the same
information. Please shorten.
3. In the “Discussion” I miss some points:
• I miss a better discussion of the discrepancy between the low BMI and high
energy intake in women. Why do you think the energy expenditure in is higher
and BMI lower in women with IBS? Are they more physically active, do they have
a slight malabsorption or hyperthyreoidisme?
• I also miss a discussion of the discrepancy between this study which shows that
the food intake is adequate, and other studies which clearly show that a
proportion of the subjects have an inadequate diet. Your results probably apply
only to subjects with IBS in the general population, whereas a significant
proportion of subjects with IBS seen at gastroenterological units have
malnutrition. Please discuss this discrepancy.
• You have performed multiple testing, why not correct the level of significance
(e.g. Bonferroni correction)?
4. Table 1 describes IBS Type A, C and D without any explanation.
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-11-9 (2011)

Reviewer's report
Title:Dietary intakes in people with irritable bowel syndrome
Version: 2Date:16 December 2010
Reviewer: Christine Dancey
Reviewer's report:
The authors have replaced most instances of the word "subjects" with
"participants", but I suggest they do a "find and replace", as I found two instances
of "subjects" (page 3 and 5) which haven't been replaced. There may be more. It
could be confusing to have both terms used.
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-11-9 (2011)

Reviewer's report
Title:Dietary intakes in people with irritable bowel syndrome
Version: 2Date:17 December 2010
Reviewer: Stine Störsrud
Reviewer's report:
The author(s) havre responded to most of the reviewers comments and I find the
article much better. The result part is much easier to read and to follow. Better
tables with p-values included!
However a few further comments:
1. IBS sufferers should be replaced by IBS subjects or IBS patients as many of
them really don´t suffer.
2. Abstract, Methods: you end the last line with "...between IBS subtypes and."
Something is missing.
3. Abstract, Results: ".....IBS sufferers met recommendations". Which
recommendations, specify! I also think you should point out that "intakes of
micronutrients exceeded the reference nutrient intake" - instead: statistically
exceeded
4. Inclusion of references on page 4: [6],[7]...[8],[9] and later on the same page
[8, 10-11] and [13-14]. You have to choose how to present, I prefere [6-7].
5. Discussion: During your disscussion you assume that IBS subjects avoid
certain foods and are therefor at risk of lower intake of energy and/or nutrients
and you write on line 1 and 2 in your discussion: The purpose of our study was to
assess.... and whether any alteration in dietary pattern...." What do you know
about whether or not the IBS patients had altered their dietary pattern. I think the
four last lines on page 13 ("Further analysis of the diet is needed to identify
whether specific food items ... are avoided") are very important and should be
included earlier in the discussion.
6. In the second part of the discussion you write about BMI, which differs
between the IBS subjects and the general population. Females with IBS have a
lower BMI, however higher intake of energy than the female gerneal population
with an energy intake of only 6,5 MJ. Could this be due to that female general
population underreport their intake, not only that female IBS underreport their
weight or have a higher energy expenditure?
7. You write on page 12 that "the FFQ used...tends to overestimate dietary
intakes...", however this is hard to believe according to the energy intake of the
female general population. Since the FFQ used in the studies is equivalent with
only minor modifications the overestimation of energy and maybe also fruit and
vegetables should be the same groups?
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-11-8 (2011)

Reviewer's report
Title:Primary Placement Technique of Jejunostomy Using the Entristar
Skin-Level Gastrostomy Tube in Patients with Esophageal Cancer.
Version: 3Date:4 August 2010
Reviewer: Ciro Esposito
Reviewer's report:
This is an interesting paper focused on jejunostomy placament in pts with EC.
As this paper shows, there are few devices created by companies to perform
jejunostomy, in fact the authors used a gastrostomy device in their study. Please
explain this point in the text.
As for the results section can be useful for the readers to know more info as for
your protocol of realimentation (how many hours per day ?, amount ?)
As for complications of your series, they were managed non operatively and how
? Explain better this point in the text.
Have you recorded episodes of vomit in the first post-operative period ?
Some centers prefer to perform jejunostomy via laparoscopy, what do you think
about ?
What do you think of the gastro-jejunal feeding tubes compared with the
jejunostomy tube ?
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-11-8 (2011)

Reviewer's report
Title:Primary Placement Technique of Jejunostomy Using the Entristar
Skin-Level Gastrostomy Tube in Patients with Esophageal Cancer.
Version: 3Date:27 September 2010
Reviewer: Charles Y Kim
Reviewer's report:
In this manuscript, the authors report their experience with inserting a skin-level
jejunostomy tube in 16 patients. Their main goal is to described their success
rate and complication rate. I believe that the primary factor making this report
unique, is that they are inserting the skin-level J-tube primarily, instead of as a
staged procedure. (This should be emphasized by the authors). The insertion of
skin-level gastrostomy and jejunostomy tubes has been in use for several
decades, and has been described in much larger patient populations. The
authors found a high success rate and low complication rate, with a median
follow up of 3.5 months. I feel that their conclusion is a bit overstated. It is difficult
to make such a strong statement after only 16 patients, and with relatively short
followup. Overall, this early experience with primary insertion of a skin-level
jejunostomy tube is helpful to readers, to encourage further exploration of this
technique.
Major compulsory revisions:
1. For two patients, the disposition of the tube is missing from the Table and in
the text. If this is because the patient was lost to follow up, this should be clarified
in the manuscript.
2. The last sentence of the M&M is unclear. If there is published data, it should
be referenced.
Minor essential revisions:
3. The grammar throughout the majority of the manuscript is in need of
correction. Several typographical mistakes are also present.
4. The use of the term G-tube and J-tube in the manuscript are confusing. It is
difficult to convey the fact that a G-tube is being used as a J-tube, but since it is
being functionally used as a J-tube, it should be referred to as a jejunostomy
tube. (except in the materials and methods section ,where its nature as a G-tube
should be mentioned.)
5. Reword the conclusion as above.
Discretionary revisions:
6. Emphasize that the unique aspect of this manuscript is the fact that the
skin-level jejunostomy tube is being inserted primarily (instead of staged).
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-11-8 (2011)

Reviewer's report
Title:Primary Placement Technique of Jejunostomy Using the Entristar
Skin-Level Gastrostomy Tube in Patients with Esophageal Cancer.
Version: 4Date:29 November 2010
Reviewer: Charles Y Kim
Reviewer's report:
The authors have done a good job revising the manuscript in response to the
initial stated issues. The topic is an important one, which I do feel adds
significantly to the body of related literature. However, I feel that the grammar
and spelling still needs to be improved prior to publication. For example, in the
first page:
The grammar of the title needs to be corrected – the use of the term jejunostomy
is not correct in this sentence.
ABSTRACT:
The use of the term “skin-level jejunostomy procedure” could be more accurately
described as a “skin-level jejunostomy tube procedure” or “skin-level transjejunal
feeding tube procedure.” Simply stating 'jejunostomy' is confusing because the
term is more commonly used to describe a loop jejunostomy.
The first sentence in the Materials and Methods section is not a sentence, it is a
sentence fragment. (there is no verb).
Jejunostomy techniques: such a detailed description is not customarily present in
an abstract. “A purse string suture of one stitch” is grammatically incorrect. A
suggestion would be “A single purse string suture”…
Results: The first sentence should clarify that the “skin-level G-tube” was
successfully inserted into the jejunum. In the last sentence, it should read “There
were no cases of obstruction of the tube OR procedure-related death.” The word
‘and’ was incorrectly used instead of ‘or’.
Discussion. This is customarily titled “Conclusion” or “Summary”. The use of the
word ‘that’ is inappropriately used. The word ‘and’ would be a better choice of
words.
There are more grammatical and spelling errors in the rest of the document. It
may be helpful to hire a professional manuscript editor to correct these. I do hope
you pursue these grammatical changes, because it will make the article much
more helpful and readable, and I do hope to see your manuscript published.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-11-6 (2011)

Reviewer's report
Title:Effect of the mode of delivery on Crohn's disease; results from a
retrospective cohort study
Version: 1Date:2 June 2010
Reviewer: Olof Stephansson
Reviewer's report:
Thank you for the opportunity to review the manuscript. This is a retrospective
study on 114 women with Crohn’s disease investigating whether mode of
delivery and episiotomy influence disease progression after pregnancy.
In general this is a well conducted study, the statistical methods and
interpretation of data is appropriate. The main concern is the limited size of the
study and whether the data reflects recent clinical practice. Furthermore are the
results due to differences in year of delivery between the groups of women with
Crohn’s disease?
Major Compulsory Revisions
1. The median interval between questionnaire and delivery was 10 years with a
range between 1-39 years. This means that the clinical practice for both Crohn’s
disease and obstetrics have changed during the study period. Could this
influence the findings? Have the authors performed any analyses on the most
recent part of the dataset? Did year of delivery differ between the groups
studied?
2. What was the median time from diagnosis of Crohn’s disease and delivery of
the index child? Did disease duration influence the findings?
3. Some women may have become pregnant during follow up. Did this alter the
results? Could this introduce bias?
Minor Essential Revisions
1. OR in tables 2-4 should be omitted and presented in the results section results
only.
2. There is no information on analysis for OR calculations in the Methods section.
P6 Statistical analysis.
3. Could the authors expand on how episiotomy could prevent perianal disease
in the Discussion, P12, L17
4. Last sentences of conclusion, P14 is rather strong given the retrospective
study design.
5. Could the authors please further discuss recall bias and confounding by
indication and how this would influence the findings?
6. How was intrauterine growth restriction and pregnancy induced hypertension
(P5, L7) defined?
7. Could the lower birth weight among women with active disease be attributed to
the difference in distribution of gestational age – 39 vs. 40 weeks of gestation?
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-11-6 (2011)

Reviewer's report
Title:Effect of childbirth on the course of Crohn's disease; results from a
retrospective cohort study in the Netherlands
Version: 2Date:12 September 2010
Reviewer: Olof Stephansson
Reviewer's report:
Regarding review of manuscript entitled 'Effect of childbirth on the course of
Crohn's disease; results from a retrospective cohort study in the Netherlands'.
The authors have responded to my questions and suggestions and I am
confident with the manuscript in its present form.
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-11-6 (2011)

Reviewer's report
Title:Effect of childbirth on the course of Crohn's disease; results from a
retrospective cohort study in the Netherlands
Version: 2Date:21 September 2010
Reviewer: Yi-Hua Chen
Reviewer's report:
No further issue rasied. Thank you.
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-11-7 (2011)

Reviewer's report
Title:Helicobacter pylori infection and circulating ghrelin levels - A systematic
review
Version: 1Date:28 April 2010
Reviewer: Peter C Konturek
Reviewer's report:
The article can be accepted without revision.
Level of interest: An article of outstanding merit and interest 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-11-7 (2011)

Reviewer's report
Title:Helicobacter pylori infection and circulating ghrelin levels - A systematic
review
Version: 1Date:12 May 2010
Reviewer: Guillermo Ignacio Perez-Perez
Reviewer's report:
The manuscript of Nweneka & Prentice entitled "Helicobacter pylori infection and
circulating ghrelin levels- A sytematic review" reported a meta analysis of several
studies that reported ghrelin levles in H. pylori positive and negative subjects.
The main goal of this analysis was to determine whether an association exists
between ghrelin and H. pylroi and in what direction.
I noticed that the authors included all the papers that measured ghrelin butthey
never mentioned if ghrelin was measured pre- or post-meal. It is well known that
ghrelin circulating values change dramatically from fast to post meal or induced
by meal.
Perhaps most of the discrepancy in the results reported is the result of this
variations.
The authors need to make more emphasis in the methods used to assess the
circulating ghrelin
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-11-7 (2011)

Reviewer's report
Title:Helicobacter pylori infection and circulating ghrelin levels - A systematic
review
Version: 1Date:8 July 2010
Reviewer: Lorenzo Fuccio
Reviewer's report:
Major Compulsory Revisions
1.Authors should follow the PRISMA Statement for reporting their meta-analysis
2.The Authors performed a wide and comprehensive literature search, however it
was only limited to English-language publications; this limitation should be stated
in the Discussion section.
3.Statistical methods for evaluating the presence of heterogeneity between
studies do not replace a qualitative assessment of the included studies; all the
included studies seem to be highly heterogeneous according to several items
(design, population, age, method of H.pylori assessment, type of sample used,
etc), therefore any conclusion should be taken with caution; furthermore, the
Authors should consider whether a qualitative rather quantitative analysis should
be preferred. Finally, random rather than fixed effect model should be preferred.
4.Publication bias was only graphically assessed; I suggest to add also a
quantitative evaluation (Begg and Egger tests), since only graphical methods are
less accurate; furthermore, a comment on this issue should be added to the
discussion.
5. The Authors avoid any evalutaion on the study quality; this choice should be
commented or a qualitative assessment should be performed
6. A paragraph suggesting the implications for research and practice should be
added to the discussion section
The quality and the usefulness of a meta-analysis depends on the quality and
homogeneity of the included studies; in order to avoid any misleading conclusion,
the Authors of a meta-analysis should always clearly state all the limitation of
their meta-analysis; although the Authors of the current analysis do not draw any
firm conclusion, however a paragraph in which all strength and limitations are
stated is lacking.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-11-7 (2011)

Reviewer's report
Title:Helicobacter pylori infection and circulating ghrelin levels - A systematic
review
Version: 2Date:30 November 2010
Reviewer: Barbara Nawrot
Reviewer's report:
The authors properly corrected the issues addressed in my previous review.
NOw manuscript is ready for acceptation.
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-11-7 (2011)

Reviewer's report
Title:Helicobacter pylori infection and circulating ghrelin levels - A systematic
review
Version: 2Date:3 December 2010
Reviewer: Lorenzo Fuccio
Reviewer's report:
The manuscript has been substantially improved and I have no major comments
to provide but just some minimal changes to suggest:
1) Heterogeneity was also evaluated with the Higgins test however the Authors
do not included this test in the methods.
2) Introduction section: please add some references on the following sentences:
“Subsequently a number of other papers, including animal studies, have explored
this relationship [REF]. A number of review articles have also appeared exploring
this relationship [REF].”
3) The results section is not always easy to read; please consider to avoid to
repeat data already reported in the tables and just limit to focus on data
considered important for the discussion and the comprehension of the topic.
4) Please consider to shorten the discussion section.
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-11-5 (2011)

Reviewer's report
Title:Computational Prediction and Experimental Validation Associating FABP-1
and Pancreatic Adenocarcinoma with Diabetes
Version: 1Date:19 September 2010
Reviewer: Per Bendix Jeppesen
Reviewer's report:
The paper is well written and clear in its message. The data are very interesting
and will give us new important knowledge about how we in the future may predict
harmful cancer diseases.
However, I find the results are very descriptive even the authors mention that this
is the first study to attempt FABP-1 association for pancreatic Adenocarcinoma.
You may also ask if the numbers of sample (patents) is high enough to make the
statement that the authors do in this paper. Overall, I admits the importance of
this study, as a possible new instrument to detect this severe fatal disease.
As a pilot study, I think the paper should be accepted as a short communication,
and then later, when new and more maintenance definitive data are ready.
Minor Essential revisions:
1) P 6 L4. Should be [11, 12]
2) Is there a reason why the authors don’t use Type 2 Diabetes instead of
Diabetes mellitus.
3) P 15 L 17. Should be [3]
4) Would be nice if you could corrects for the age difference between normal and
cancer group, as we know that type 2 diabetes is offend are related to age.
5) Further explanations needed for fig 2. Please illustrate on the pictures, the
main differences.
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' below
Review for 10.1186/1471-230X-11-5 (2011)

Reviewer's report
Title:Computational Prediction and Experimental Validation Associating FABP-1
and Pancreatic Adenocarcinoma with Diabetes
Version: 1Date:27 September 2010
Reviewer: Juergen Schrezenmeir
Reviewer's report:
The manuscript RN Sharaf et al. is interesting, but still has some draw backs
which require major compulsory revisions.
The methodology of search for candidates resulting in FABP1 should be
described more precisely to enable understanding the process of data analysis
and the results of this search should be given in detail to enable understanding
the basis of candidate selection. What was the scoring of FABP1 (between the
given range of +1.0 and -1.0) compared to other genes, what was the ranking
compared to other genes?
To further elucidate, whether diabetes may have been more or less likely to be
associated with FABP1 expression by tumor tissue, the duration of diabetes in
the 13 diabetes cases (based on patient’s histories) would be interesting to know.
Furthermore the grade of infiltration of the pancreas of the cases without
compared to the cases with diabetes would be of interest, since diabetes might
be due to the grade of infiltration, which may be related to the grade or kind of
differentiation (that may be related to FABP1 expression).
FABP1 is suggested to be involved in the pathogenesis of diabetes via facilitating
fat uptake, cellular trafficking, and chylomicron/VLDL production. This seems
unlikely to take place to a significant extent in pancreatic tumor tissue, which is
supplied by the nutrients via the portal vein. Therefore a secondary mechanism
should be suggested in case the findings may be confirmed in later studies.
Pg. 6
Which microarrays were used? (human genome wide? Which supplier?).
The authors state that a measure ranging from +1.0 (highest value found in
pathologic tissue) to -1.0 (lowest value in normal tissue) was used to rank the
genes expressed in diseased samples.
This score should be given in the results as well as the scores of the other 10
genes ranking close to (higher and/or lower than) FABP1.
It is confusing that this measure evidently was not used as stated, but a
comparison with pancreatitis and type 1 diabetes samples was used for
selection.
The sentence “we crossed the list” should be rephrased more precisely. Down to
which RR or OR was this “crossing” done?
Pg 7
The first sentence “given the beta cell …” is not clear.
Were all genes associated with DM or only those which were associated with
beta-cell function and insulin resistance in pancreatic carcinoma?
Why are type 2 diabetes susceptibility genes separately mentioned?
Pg 15
Last sentence: “to have”
Pg 16
Better rephrase:
“Only one pathologist scored immunohistochemistry. He, however, has several
years of experience.”
Table 1
The diabetes prevalence of 21% is in contrast to published data (45-65%). This
should be discussed by the authors.
Review for 10.1186/1471-230X-11-5 (2011)

Reviewer's report
Title:Computational Prediction and Experimental Validation Associating FABP-1
and Pancreatic Adenocarcinoma with Diabetes
Version: 2Date:29 December 2010
Reviewer: David Morse
Reviewer's report:
All of my comments and recommended revisions have been sufficiently
addressed by the authors.
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-11-5 (2011)

Reviewer's report
Title:Computational Prediction and Experimental Validation Associating FABP-1
and Pancreatic Adenocarcinoma with Diabetes
Version: 2Date:6 January 2011
Reviewer: Juergen Schrezenmeir
Reviewer's report:
I read the comments and the revised manuscript.
My original criticicms have been answered.
Review for 10.1186/1471-230X-11-4 (2011)

Reviewer's report
Title:Likelihood of complete response for advanced liver cancer during sorafenib
therapy: Case Report
Version: 2Date:15 September 2010
Reviewer: Petros PG Giovanis
Reviewer's report:
Discretionary Revision: it could be interest to report if the patient presented any
comorbidity and/or assumed any concomitant medication.
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-11-4 (2011)

Reviewer's report
Title:Likelihood of complete response for advanced liver cancer during sorafenib
therapy: Case Report
Version: 2Date:17 September 2010
Reviewer: Ferry ALM Eskens
Reviewer's report:
Case report indeed describes an unusual case of seemingly CR of HCC following
exposure to sorafenib.
The case is somewhat incomplete, as we are not informed about the duration of
this CR; no follow-up after the "diagosis" of CR was made is given; how long is
the response lasting, is patient still on drug or did the authors decide to
stop/interrupt treatment ( a kind of stop-and-go approach); was follow-up
scanning performed?
The title is strange; this IS a CR, so why mention likelihood; it is an observation
that was made.
There are no pagenumbers.
Introduction/case presentation; linguistically this needs corrections (addiction
should be read as addition (at least I hope so) and should be restricted to HCC
and sorafenib treatment (results) and a relevant description of the case.
While describing the work up of this patient; upper digestive tract endoscopy
suffices, no need to mention what was scopied; in addition it is hard to believe
that the jejunum was reached.
Why specifically mentioning cardiac evaluation (without mentioning what was
done)
Was a screening bone scan performed?
What is the relevance of CA19.9 in the diagnosis HCC (and the FU during
treatment)
Concomitant HCV infection should be read as underlying HCV infection.
The paragraph of the metalloproteinase inhibitors is incomplete; which MPI was
measured; more references would be helpfull in asseseing their role; there only
seems to be a small decrease in the levels during treatment; what are noral
levels, and again what lead to the decision to measure this level (of which MPI);
how relevant is this and does it add to any evidence of activity of sorafenib (and if
so by which mechanism)
Reference 7 has long been published in the Lancet
The figure legend is incorrect
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-11-4 (2011)

Reviewer's report
Title:Likelihood of complete response for advanced liver cancer during sorafenib
therapy: Case Report
Version: 2Date:20 September 2010
Reviewer: Lorenza Rimassa
Reviewer's report:
The paper reports a case of complete response to sorafenib in a patients with
advanced HCV-related hepatocellular carcinoma.
Notwithstanding the limits of a case report, it could be of some interest due to the
few published data, the limited therapeutic options and the poor prognosis of
these patients.
The Authors point out and argue some interesting aspects of this case, as the old
age of the patient, the achieved complete response, the good tolerability of
sorafenib, the activity of the drug on the portal vein thrombosis and the reduction
of metallo-proteinase serum levels during the treatment. A minor limit of this case
is the lack of a tumor biopsy at diagnosis and during the treatment.
Minor Essential Revisions
The main limit of this paper consists in the English language that does not seem
very accurate and needs an extensive editing.
In conclusion, I think the paper could be of some interest but it needs major
editing review before it could be published.
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-11-4 (2011)

Reviewer's report
Title:Likelihood of complete response for advanced liver cancer during sorafenib
therapy: Case Report
Version: 2Date:23 September 2010
Reviewer: GHASSAN ABOU-ALFA
Reviewer's report:
This is a case report of a patient with a complete response allegedly secondary
to sorafenib.
Minor but essential revisions:
The authors present a well written manuscript and report clearly the limitation of
their evaluation, especially the lack of a biopsy. They should however report in
the case presentation which diagnostic criteria were used and if they were all
met.
The authors bring up in the discussion another variable about the age of the
patient and tolerability of the drug. As this is not the subject of discussion and
patients are prescribed cancer care based on performance rather than age, it is
suggested to tone down this piece
However a more important piece about sorafenib effect on modulation of
pro-thrombotic cytokines should be elaborated on further
Lastly it would be valuable if the authors comment on the status of the arterial
vasculature as resolution of liver masses accompanied by the development of an
arterial thrombus is well noted in the literature.
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:
- Have you in the past five years received reimbursements, fees, funding, or
salary from an organisation that may in any way gain or lose financially from the
publication of this paper, either now or in the future?
Yes research support from Bayer
Advisory to Bayer
Review for 10.1186/1471-230X-11-4 (2011)

Reviewer's report
Title:Complete response for advanced liver cancer during sorafenib therapy:
Case Report
Version: 3Date:29 October 2010
Reviewer: Ferry ALM Eskens
Reviewer's report:
Major Compulsory Revisions
Somewhat disappointingly, there still is no single indication of duration of
response, and I cannot imagine that no follow up CT or MRI scans have
meanwhile been performed assessing the CR that likewise has been diagnosed
in mid 2010 (june/july?)
There is also no FU on MMP 9 levels and still no mentioning of 'normal' plasma
levels making it impossible to assess and interpret the changes
I question the paragraph describing the role of sorafenib on portal thrombosis; I
presume there was tumouringrowth and not so much venous thrombosis as such
(because if it were venous thrombosis the patient initially should and could have
been considered for primary resection)
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-11-4 (2011)

Reviewer's report
Title:Complete response for advanced liver cancer during sorafenib therapy:
Case Report
Version: 4Date:17 December 2010
Reviewer: Ferry ALM Eskens
Reviewer's report:
I still think this report is of limited importance, but a case history it can be
considered for publication after linguistic revision with special emphasis on the
sometimes poor grammar.
Review for 10.1186/1471-230X-11-3 (2011)

Reviewer's report
Title:Distribution of enteric glia and GDNF during gut inflammation
Version: 1Date:2 November 2010
Reviewer: Robert Ehehalt
Reviewer's report:
Dear Editor,
The manuscript "Distribution of enteric glia and GDNF during gut inflammation" is
quite interesting. The authors have used human material and could show
differences in different inflammatory disease of the gut. This makes their
investigations in general worth for publication.
However, I suggest the following revisions:
1. Discretionary Revisions:
a. Figure 1 need a better solution for review
b. Where biopsies taken from inflamed and non-inflamed areas of the same
patients? If yes, it would be quite interesting how the intrainduvidual variation
would be. I could imagine that some patients respond stronger than others.
2. Minor Essential Revisions:
a. Discussion: What does the authors mean with adequate and inadequate
secretion? Because there is no correlation to the amount of inflammation I would
suggest being more neutral in the statement.
b. For the semi-quantitative analyses it would be helpful also to show exemplarily
a Western-blot to estimate how solid the quantification can be.
c. How many biosies were taken per patient?
3. Major revisions:
a. The picture quality of figure 1 is to low to make an adjustment. Please provide
figures with a better solution.
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'