JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-5-14 (2005)

Reviewer's report 
 The accuracy of the report of hepatic steatosis on ultrasonography in a clinical setting: A Title: 
retrospective observational study 
 1  2 December 2004 Version: Date: 
 Bruce A Runyon Reviewer: 
Reviewer's report: 
General 
This is a "real-world" study of the sensitivity and specificity of ultrasound in detecting steatosis in the 
setting of hepatitis C, with biopsy as the gold standard. 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
1. Hepatitis C should be included in the title. 
2. It would make the most sense to include only patients with ultrasound and biopsy (122). Why 
include those who had no biopsy? 
3. The ultrasound equipment used should be stated. Some equipment may be preferable to others 
for this purpose. 
4. Were there patients with focal fatty liver or focal fatty sparing? If so, was the biopsy directed? 
5. What was the interval from ultrasound to biopsy? If it was long, weight change during that interval 
would be relevant. 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) 
None 
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Discretionary Revisions (which the author can choose to ignore) 
1. The authors may want to mention other imaging modalities that are better than ultrasound in 
detecting fat. 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-14 (2005)

Reviewer's report 
 The accuracy of the report of hepatic steatosis on ultrasonography in a clinical setting: A Title: 
retrospective observational study 
 2  9 March 2005 Version: Date: 
 Bruce A Runyon Reviewer: 
Reviewer's report: 
General 
Th is now acceptable. ------------------------------------------------------------------------------- Major Compulsory Revisions (that the author must respond to before a decision on publication can 
be reached) 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) 
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Discretionary Revisions (which the author can choose to ignore) 
 Accept without revision What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competeing interests.
Review for 10.1186/1471-230X-5-13 (2005)

Reviewer's report 
 Hepatocyte growth factor (HGF) in fecal samples: rapid detection by surface plasmon Title: 
resonance 
 1  20 August 2004 Version: Date: 
 Wen W.G. Jiang Reviewer: 
Reviewer's report: 
General 
The study describes the development of a new method, surface plasmon resonance, to detect human hepatocyte growth factor in clinical samples. It is interesting in two folds, first, it provides a new tool in analysing HGF; second, it appears to be reliable applicable to difficult samples, i.e. fecal 
samples which are notoriously difficult to study. From this point of view, the manuscript should be of 
good interest to those who work in this area. 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can 
be reached) 
My major concern is the size of the sample numbers in each of the three groups. For example, there 
are only 9 in control and 6 in cancer group. There was no indication of logics and selection criteria in 
choosing the patients. Clinical description is important in both gasteroenteritis and cancer groups, as 
it has important bearings to the enterpritation of the findings. 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) Figures and lengends are generally well organised and easy to understand. 
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Discretionary Revisions (which the author can choose to ignore) 
 Accept after minor essential revisions What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Needs some language corrections before being published Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
None
Review for 10.1186/1471-230X-5-13 (2005)

Reviewer's report 
 Hepatocyte growth factor (HGF) in fecal samples: rapid detection by surface plasmon Title: 
resonance 
 2  18 February 2005 Version: Date: 
 Michael Pearce Reviewer: 
Reviewer's report: 
The results generated by the experiments are surface plasmon 
resonance signals and optical density readings from ELISA. Both types of data are continuous but may well not be normally distributed. The authors appear to have taken a conservative 
approach and used non-parametric statistical techniques which is 
sensible. 
The numbers of patients and controls in the study is small. This 
can result in inadequate statistical power, but the authors seem 
to have achieved a number of statistically significant results 
which suggests that statistical power is not a major issue. 
However, with small numbers, results are inherently unstable and 
it would be useful if the authors could give some indication of 
just how variable results for PSR and ELISA were by tabulating 
results. Because of the small sample size, selection biases may 
also be important determinants of results in this study. 
In RESULTS, para 1, the authors state that patients with 
gastroenteritis had significantly higher signal responses compared with patients with colon cancer or normal controls. 
They should say what statistical technique they used to come to 
this conclusion. 
The authors demonstrate a correlation between SPR and ELISA 
results for patients with gastroenteritis. However, as a rule of 
thumb, one should have 10 or more points for regression lines/curves. Figure 3 does not meet this criterion. 
The use of the Friedman test and Wilcoxon test to assess the 
effects of altering the immobilization levels is appropriate. 
In Figure 1, the confidence limit for SPR readings for samples 
from patients with colonic cancer is <0. 
The authors concede in the DISCUSSION that the number of 
observations is small but then state they have results of 
significance from another study with 70 patients. Why not 
combine the results for a much more robust paper? If there is some urgency about reporting results from the smaller study, I think it would be appropriate for the authors to consider a 
letter or small communication format, and submit a more formal 
paper later with results from both studies.
Review for 10.1186/1471-230X-5-13 (2005)

Reviewer's report 
 Hepatocyte growth factor (HGF) in fecal samples: rapid detection by surface plasmon Title: 
resonance 
 2  15 March 2005 Version: Date: 
 Wen W.G. Jiang Reviewer: 
Reviewer's report: 
The authors have made some substantial revisions and have answered most of my concerns. I am 
happy in recommending to publish the revised version in the BMC Gastrenterology. 
 Accept without revision What next?:
Review for 10.1186/1471-230X-5-12 (2005)

Reviewer's report 
 Epidermal growth factor mediates detachment from and invasion through collagen I and Title: 
Matrigel in Capan-1 pancreatic cancer cells 
 1  24 October 2004 Version: Date: 
 Jorg Kleeff Reviewer: 
Reviewer's report: 
'Epidermal growth factor mediates detachment from and invasion through collagen I and Matrigel in 
Capan-1 pancreatic cancer cells ' BMC Gastroenterology 
The study by Shirk and Kuver examines the role of EGF on invasion and adhesion in Capan-1 
pancreatic cancer cells. The authors demonstrate that there is an inverse relationship between the invasion and adhesions capabilities and that these events are mediated by EGF receptor signalling involving the erbB2 and PI3K pathways. 
This is an interesting study and the experimental procedures are in general sound and valid. 
Although most of the aspects of the present study are not completely novel and have been 
described in other cell system, the present paper adds some novel information regarding the role of 
EGF in pancreatic cancer. There are, however, certain points that should be addressed: 
Major Compulsory Revisions 
• The authors utilized only a single pancreatic cancer cell line (Capan-1) to analyze the effects of EGF on invasion and adhesion. It would be important to use at least one additional pancreatic 
cancer cell line and perform some of the key experiments in this cell line. 
• The authors should provide information regarding the expression levels of all (!) four EGF receptors 
in the analyzed cell lines. This information is crucial especially regarding the final conclusion of the 
present paper. It would be interesting to perform this analysis quantitatively (e.g. immunoblotting). 
• The authors utilized EGF and for some additional experiments also heregulin-alpha. The rationale 
for using this (and not other) growth factors of the EGF family is not clear and should be elaborated. • The authors speculate that EGF acted via erbB1 and erbB2 and heregulin via erbB3 and erbB4. However, the authors do not provide any good experimental evidence for this conclusion. The 
authors should either demonstrate for example the activation/phosphorylation of the respective 
receptors in response to the growth factors or analyze the effects of specific blockage of these receptors. • In this context, for further experiments, the authors utilized erbB2 and erbB3 inhibitors /receptor 
antibodies. The authors should also analyze EGFR inhibitors /receptor antibodies for these 
experiments. 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
None
Review for 10.1186/1471-230X-5-12 (2005)

Reviewer's report 
 Epidermal growth factor mediates detachment from and invasion through collagen I and Title: 
Matrigel in Capan-1 pancreatic cancer cells 
 1  26 November 2004 Version: Date: 
 Surinder Batra Reviewer: 
Reviewer's report: 
General 
Reviewer's report: The manuscript entitled "Epidermal growth factor mediates detachment from and invasion through collagen I and Matrigel in Capan-1 pancreatic cancer cells" by Shirk and Kuver, is 
is well-written and easy to follow. The authors hypothesized that EGF receptor and integrin signaling 
pathways interacted in mediating cellular adhesion and invasion in pancreatic cancer, and that 
invasiveness correlated with cell detachment from the extracellular matrix. Using the pancreatic tumor cell line, Capan-1, as a model system, the authors examined the role of EGF in mediating 
adhesion to and invasion through collagen I and Matrigel. They found that adhesion to collagen I and 
Matrigel could be inhibited by EGF treatment. Moreover, this loss of adhesion could be reversed by 
inhibitors of PI3K and erbB2 receptor signaling, but not by an inhibitor of protein synthesis. 
Although the process of EGF-induced de-adhesion in Capan-1 cells per se is not novel (ref. 26), the 
data presented brings new insights into the underlying mechanisms. This reviewer feels the paper is 
suitable for publication contingent upon completion of the changes requested below: 
1) The statement Ã¢â‚¬Å“The inhibition of adhesion to collagen I elicited by EGF acted specifically via activation of erbB1Ã¢â‚¬Â¦Ã¢â‚¬Â  in Results is not supported by the data in this section and 
should be moved over to the next section. 
2) The concentrations of inhibitors used should be provided as they may have an impact on the 
interpretation of the data. This is particularly relevant to those for which no conspicuous effect was observed, since no control has been used to test the efficacy of the reagent(s). 3) Paragraph #1 in the Discussion: The statement "The lack of EGF secretion by these cells 
suggests that the drive to invasiveness in these cells is provided by cell-cell interactions" is not 
supported by the data presented in the paper as no targeted inhibition of EGF (e.g., silencing by siRNA) has been used to prove that the invasiveness seen in the unstimulated control is indeed attributable to EGF (Fig. 3). i.e., EGF may just enhance the invasive potential of the cells. 
4) A major point made on the activation of FAK in the Discussion section is not supported by any 
result in this manuscript. 5) No attempt is made in the Discussion to explain the differences in the results observed by the authors and other investigators (Ref. 26) although the same experimental system was used.
Review for 10.1186/1471-230X-5-12 (2005)

Reviewer's report 
 Epidermal growth factor mediates detachment from and invasion through collagen I and Title: 
Matrigel in Capan-1 pancreatic cancer cells 
 2  16 December 2004 Version: Date: 
 Jorg Kleeff Reviewer: 
Reviewer's report: 
The authors responded adequately to the criticism of the reviewer 
 Accept without revision What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review:
Review for 10.1186/1471-230X-5-12 (2005)

Reviewer's report 
 Epidermal growth factor mediates detachment from and invasion through collagen I and Title: 
Matrigel in Capan-1 pancreatic cancer cells 
 2  17 January 2005 Version: Date: 
 Surinder Batra Reviewer: 
Reviewer's report: 
The revised manuscript has clarified several points raised by the reviewers in the first submission. 
As pointed by other reviewer and the authors, there are differences between various reports on the 
expression of EGFR1 and EGFR2 in Capan 1 cells; therefore, it is important to show their 
expression, including EGFR3 and EGFR4 in these cells (including MiaPaca) in this manuscript. 
Additionally, a large number of Figures are included in this manuscript and can be reduced. Figure 
10 and 11 can become part of Figures with Capan 1. There are different nomenclature, for example, 
vehicle, no treatment or control. It should be same for clarity. Results on MiaPaca should be 
integrated with Capan 1 and explanations should be provided for differences on the percentage of 
adhesion values. In summary, the manuscript is recommended for publication contingent upon completion of the changes requested above.
Review for 10.1186/1471-230X-5-11 (2005)

Reviewer's report 
 The relation between plasma tyrosine concentration and fatigue in primary biliary cirrhosis and Title: 
primary sclerosing cholangitis 
 2  12 December 2004 Version: Date: 
 Daniel Forton Reviewer: 
Reviewer's report: 
General 
Although the authors have attempted a very full rebuttal, I remain unconvinced about the central 
conclusion that fatigue in PBC is related to somehow discrepantly normal tyrosine levels. The 
cause(s) of fatigue in PBC and PSC are likely to be the same, yet no relationship between tyrosine 
and fatigue was observed in the PSC group. This has not been discussed. 
Furthermore, the authors base the rationale for this study on previous reports of a correlation 
between elevated tryptophan and fatigue in non-hepatic conditions. The opposite results in this study 
in the PBC group again have not been discussed. 
I am still of the opinion that the data in this study are not internally consistent and that it is difficult to 
draw any conclusions regarding fatigue and amino acid levels in these patients groups. I acknowledge that the authors have qualified their conclusions with a number of caveats. 
Since the tyrosine levels in the PBC group were not low (the fatigued PBC patients still had a higher 
mean tyrosine level than the controls) all references to low tyrosine levels should be corrected to normal tyrosine levels. 
The legend for table 3 appears incorrect 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can 
be reached) 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review:
Review for 10.1186/1471-230X-5-11 (2005)

Reviewer's report 
 The relation between plasma tyrosine concentration and fatigue in primary biliary cirrhosis and Title: 
primary sclerosing cholangitis 
 2  22 December 2004 Version: Date: 
 U Leuschner Reviewer: 
Reviewer's report: 
The manuscript has been markedly improved. All recommondations have been accepted and were 
included into the revised paper. 
One thing that remains unaccounted for, is why the authors did not send the questionaires 
concerning fatigue to the 73 healthy controls and patients with chronic hepatitis C but only to 18 
other healthy individuals. Nevertheless, the paper can be accepted for publication in the revised version.
Review for 10.1186/1471-230X-5-11 (2005)

Reviewer's report 
 The relation between plasma tyrosine concentration and fatigue in primary biliary cirrhosis and Title: 
primary sclerosing cholangitis 
 5  15 February 2005 Version: Date: 
 U Leuschner Reviewer: 
Reviewer's report: 
The manuscript has been markedly improved. All recommondations have been accepted and were 
included into the revised paper. 
One thing that remains unaccounted for, is why the authors did not send the questionaires 
concerning fatigue to the 73 healthy controls and patients with chronic hepatitis C but only to 18 
other healthy individuals. Nevertheless, the paper can be accepted for publication in the revised version. 
 Accept after discretionary revisions What next?:
Review for 10.1186/1471-230X-5-11 (2005)

Reviewer's report 
 The relation between plasma tyrosine concentration and fatigue in primary biliary cirrhosis and Title: 
primary sclerosing cholangitis 
 5  23 February 2005 Version: Date: 
 Daniel Forton Reviewer: 
Reviewer's report: 
General 
The authors have qualified their conclusions with caveats and, as such, I have no further points to make prior to publication ------------------------------------------------------------------------------- 
Major Compulsory Revisions (that the author must respond to before a decision on publication can 
be reached) 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) 
 Accept without revision What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-10 (2005)

Reviewer's report 
 Persistent Demographic Differences in Colorectal Cancer Screening Utilization despite Title: 
Medicare Reimbursement 
 1  21 January 2005 Version: Date: 
 Gregory Cooper Reviewer: 
Reviewer's report: 
General 
A well written paper and well done analysis that provides more recent data on colon procedure use 
than in previous studies. 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
1. A limitation in sample selection was exclusion of a potentially large number of managed care 
enrollees, as HMO penetration in Washington is probably higher than average. Although these patients should be excluded, the number of individuals who were excluded for this and other 
indications should be cited. 
2. Another limitation of this study is the relatively small number of minorities. This becomes relevant, 
for example, in some of the multivariable analyses where the confidence intervals appear large. This 
should be acknowledged as a limitation. 
3. Given the large sample size, a smaller p value should be used as a cut off in the univariate 
analyses to determine statistical significance. 4. The cross-sectional nature of the study is also a limitation as patients who may have previously undergone screening with a procedure recommended less frequently than yearly would have been 
classified as unscreened. 
5. Potential reasons for the highest screening rates in patients aged 70-74 and urban residents should be included in the Discussion. 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
1. Abstract: Terms such as â €œinvasiveâ € and â €œscreeningâ € are used but not explained. 
2. Abstract: Data to support the first sentence of conclusions is not cited previously. 3. The term â €œscreeningâ € throughout the paper refers to both the procedural indication 
determined by diagnostic and procedure codes as well as procedure use in general. As this 
generates some confusion, would suggest using â €œscreening indicationâ € to refer to the former. 
4. Last sentence of â €œPatient Selectionâ € sentence of Methods is contradictory. 
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Discretionary Revisions (which the author can choose to ignore) 
None. 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-10 (2005)

Reviewer's report 
 Persistent Demographic Differences in Colorectal Cancer Screening Utilization despite Title: 
Medicare Reimbursement 
 1  15 February 2005 Version: Date: 
 Theodore Levin Reviewer: 
Reviewer's report: 
General 
This research has great importance for colorectal cancer screening research and policy. The finding 
of higher use of FOBT in women supports the hypothesis that FOBT screening is more attractive to 
women than men, and that the reverse is true for invasive screening (generated elsewhere: J Gen 
Intern Med. 2003 May;18(5):357-63; Prev Med. 2004 Jun;38(6):669-75). The increased use of FOBT 
in rural areas compared with colonoscopy supports the hypothesis that available screening resources is a vital predictor of colorectal cancer test use (Gastroenterology. 2004 
Dec;127(6):1841-4.). 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can 
be reached) None. 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct). 
The terms "multivariable" and "multivariate" are often used interchangeably and are both used in this paper to refer to the same thing. It is my understanding that "multivariable" refers to analyses with 
multiple predictor variables and a single outcome variable (the type described in this paper), and that 
"multivariate" refers to analyses with multiple outcome variables. This problem can be overcome by 
referring to "multiple logistic regression" to describe the analyses conducted here. 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) The authors should list the following limitations to their research: 
(1) The data analysis was limited to only a single year, 2000. A lot has changed in the colorectal 
cancer screening landscape since then (Clin Gastroenterol Hepatol. 2004 Jan;2(1):72-7. Gastroenterology. 2004 Dec;127(6):1661-9. Gastroenterology. 2004 Dec;127(6):1670-7.) 
(2) The data were limited to only a single state, Washington, which may be representative of the rest 
of the US in certain respects, but unique and unrepresentative in other respects. These specific 
areas should be explicitly stated. 
 Accept after minor essential revisions What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
Research support has been received from EXACT Sciences, Enterix, Inc, and Beckman Coulter.
Review for 10.1186/1471-230X-5-9 (2005)

Reviewer's report 
 Energy metabolism in pathological human liver Title: 
 2  24 December 2004 Version: Date: 
 Jerry Glickson Reviewer: 
Reviewer's report: 
General 
REFEREES REPORT 
Evaluation 
1. Is the question posed by the authors new and well defined? Yes 
2. Are the methods appropriate and well described, and are sufficient 
details provided to replicate the work? Yes 3. Are the data sound and well controlled? Yes 4. Does the manuscript adhere to the relevant standards for reporting and 
data deposition? Yes 
5. Are the discussion and conclusions well balanced and adequately supported by the data? Yes 6. Do the title and abstract accurately convey what has been found? Yes 
7. Is the writing acceptable? Yes 
Compulsory Revision Required No 
GENERAL CRITIQUE:. This is an exceptionally well written manuscript. The data are well presented 
and analyzed. The manuscript resolves an unsolved question in the literature and implies that the detection of CK activity in the liver or detection of PCr in 31P MRS spectra of the liver may serve as 
a index for tumor detection in that organ. In this regard it might be noteworthy that more sensitive 
methods for imaging PCr in biological tissues have recently been introduced by Greenman and Lenkinski (JMRI 15(4):467-72, 2002, Magnetic Resonance in Medicine. 39(5):851-4, 1998). This might facilitate detection of sites of PCr production (i.e., tumors) in the liver. 
The only minor fault is an attempt to rationalize the results in terms of P53 mutations. The fact that 
P53 leads to suppression of BB-CK and enhanced expression of MM-CK, does not lead to the conclusion that mutation or inactivation of this gene will produce the reverse effect. 
Recommendation 
Publication is enthusiastically recommended. These data have not been published previously as far as this reviewer is aware. Deletion of the speculative comment is recommended but not required. 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) 
Deletion of the speculative comment (on P53) is recommended but not required. 
 Accept after discretionary revisions What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests.
Review for 10.1186/1471-230X-5-9 (2005)

Reviewer's report 
 Energy metabolism in pathological human liver Title: 
 2  31 December 2004 Version: Date: 
 Michel Vaubourdolle Reviewer: 
Reviewer's report: 
General 
The authors measured total CK activity and separate CK isoenzymes in 25 samples from liver 
transplants. The work is well-conducted concerning analytical aspects. However, some major points in the 
discussion are not supported by data presented. 
------------------------------------------------------------------------------- Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
1- Liver total homogenate represents the sum of CK activities from hepatocytes and sinusoidal cells, 
which are known to be different regarding to CK isoenzymes content. Thus, it is very difficult to 
interpret results from these isolated data. It is necessary to compare these results with histochemical
data or isolated cells data. 
2- The number of patients is very weak (n=25) with a great heterogeneity. The quantitaive data are 
thus statistically not significant and interpretation of HCC occurence on CK activity cannot be 
supported (n=2) 
3- Discussion section concerning p53 and gene aspects : data presented do not support the 
discussion 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
1- Clinical data from patients are missing 
2- Paper title is not consistent with data presented 
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Discretionary Revisions (which the author can choose to ignore) 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Not suitable for publication unless extensively edited Quality of written English: 
 Yes Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-9 (2005)

Reviewer's report 
 Elevated creatine kinase activity in primary hepatocellular carcinoma Title: 
 3  24 February 2005 Version: Date: 
 Michel Vaubourdolle Reviewer: 
Reviewer's report: 
General 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
------------------------------------------------------------------------------- 
Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) * 
 Accept without revision What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
'I declare that I have no competing interests
Review for 10.1186/1471-230X-5-6 (2005)

Reviewer's report 
 A Connection between Chronic Sinusitis and Ulcerative Colitis Title: 
 1  3 November 2004 Version: Date: 
 gabriele mazzacca Reviewer: 
Reviewer's report: 
The paper of Yang et al. claims to disclose a connection between chronic sinusitis and ulcerative 
colitis. The authors tempt to show the connection either clinically or experimentally. 
However the clinical part of the study appears to be completely unsatisfactory. Two groups of 
patients with ulcerative colitis are compared. The patients of one of the two groups were affected 
also by chronic sinusitis, successfully treated with functional endoscopic sinus surgery. The authors 
state that ulcerative colitis improved in this group at 6 months after the sinusitis treatment either clinically or endoscopically, even if patients did not receive any treatment for colitis. 
Nothing is indicated with regard to sex, age, duration and extension of colitis in both groups of 
patients. Nothing is indicated about the "routine" treatment which is stated to be administered to the 
group without sinusitis ( control group ). It is very difficult to agree with the choice of the authors who 
did not prescribe any specific colitis treatment in colitis patients after sinus surgery despite the fact 
that most of them had severe-moderate colitis, according to the description of the authors. 
In conclusion this part of the study is completely unsatisfactory. 
With regard to the experimental part of the study methods and discussion of the results are not 
acceptable. Experimental colitis was induced in mice by peritoneal injection of sinus wash fluid from patients with sinusitis. The fact that the injection of the sinus wash fluid elicited colitis in the mice is claimed to disclose a connection between sinusitis and ulcerative colitis. The authors in their 
conclusion failed to consider an important aspect, that is the mice colitis induced in their study is not 
comparable to human ulcerative colitis.
Review for 10.1186/1471-230X-5-6 (2005)

Reviewer's report 
 A Murine Model of Ulcerative Colitis: Induced with Sinusitis-Derived Superantigen and Food Title: 
Allergen 
 4  20 January 2005 Version: Date: 
 Agesilao D'Arienzo Reviewer: 
Reviewer's report: 
All requests were satisfied by authors. 
In this form the paper is suitable for publication. 
 Accept without revision What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-7 (2005)

Reviewer's report 
 Antioxidant mechanisms of insulin-like growth factor-I (IGF-I) in rats with advanced liver Title: 
cirrhosis. 
 1  25 October 2004 Version: Date: 
 Jens-Gerd G Scharf Reviewer: 
Reviewer's report: 
The study by Garcia-Fernandez and co-workers aimed to study antioxidant effects of IGF-I 
administration in a rat model of liver cirrhosis. The present study follows previous publications of the authors showing a protective effect of exogenous IGF-I during experimental liver fibrogenesis. Using a rat model of CCl4 inhalation, cirrhotic animals showed increased hepatic levels of iron, copper, 
ferritin, transferrin, myeloperoxidase as well as iNOS production. Treatment of IGF-I resulted in a 
significant reduction of all these parameters. From these data the authors conclude that the beneficial effect of IGF-I treatment during fibrogenesis was associated with a reduction of the “prooxidant” and proinflammatory factors. In general, the results are of potential interest. However, 
several major points need to be addressed. 
1. Major point: In the present manuscript the authors suggest an antioxidant mechanism underlying 
the protective effect of exogenously added IGF-I during experimental liver fibrogenesis. However, 
the authors do not provide any experimental evidence for this conclusion. From the present 
manuscript it is not clear whether IGF-I really acts through antioxidant mechanisms or through other mechanisms which secondarily lead to a reduction of the above mentioned parameters. Therefore, the conclusions drawn from the experimental data in the title, abstract and discussion of the 
manuscript should be carefully revised. In addition, the term “prooxidant” given by the authors is 
misleading and should be deleted from the text. 2. Minor points: In the figure legends the authors state that iron was present in Kupffer cells (Fig. 1) and that a strong iNOS staining was detected in Kupffer cells (Fig. 2), respectively. However, the 
authors provide no experimental evidence clearly identifying KC. Therefore, further experiments are 
necessary such as immunohistology showing a colocalization with Kupffer cells specific immunostaining. 
3. In Fig.1, the Perl´s Prussian Blue staining of the healthy control group should be depicted as well. 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
none
Review for 10.1186/1471-230X-5-7 (2005)

Reviewer's report 
 Antioxidant effects of insulin-like growth factor-I (IGF-I) in rats with advanced liver cirrhosis. Title: 
 5  3 January 2005 Version: Date: 
 Jens-Gerd G Scharf Reviewer: 
Reviewer's report: 
After revision, the manuscript is now acceptable for publication 
 Accept without revision What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-7 (2005)

Reviewer's report 
 Antioxidant effects of insulin-like growth factor-I (IGF-I) in rats with advanced liver cirrhosis. Title: 
 5  17 January 2005 Version: Date: 
 Rafael Bruck Reviewer: 
Reviewer's report: 
I am satisfied with the explanations of the authors, and the changes 
they made in the paper. As the authors stated the paper is largely a 
descriptive one and some of the additional experiments suggested are for the the sake of discussion and probably performing them is beyond the scope of this interesting (although largely descriptive) work. Some of 
the suggested experiments will be subject for future studies by the 
authors, as they claimed. Minor change: In the abstract (4th line): severe should be changed to several. 
In conclusion, I recommend to accept the revised paper.
Review for 10.1186/1471-230X-5-8 (2005)

Reviewer's report 
 The role of mast cells in the pathogenesis of pain in chronic pancreatitis Title: 
 1  2 October 2004 Version: Date: 
 fred S gorelick Reviewer: 
Reviewer's report: 
General 
This study examines the relationship between pancreatic mast cells and pancreatic pain. An 
attractive feature of the study is that it combines clinical data from patients with chronic pancreatitis 
with in vivo studies in an animal model of this disease. It concludes that pancreatic mast cells are a 
determinant of pancreatic pain. 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
1) The interpretation of the abdominal pain response provided in the results section is confusing and 
seems to indicate that differences were not observed between the WT and mutant. The meaning of 
the changes shown in figure 3 need to be explained more completely - although it appears there are 
differences, it is difficult to understand their meaning - are these statistically significant changes? 
2)Table I was not included in the PDF that I received. 
3) The micrographs showing mast cells were not convincing; perhaps this is due to digitization of the image but I wonder if any special stains were used to confirm their identity? ------------------------------------------------------------------------------- 
Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the 
author can be trusted to correct) It would be worth mentioning the recent publication by this group in the Journal Gastroenterology, especially in the context of the model 
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Discretionary Revisions (which the author can choose to ignore) 
 Unable to decide on acceptance or rejection until the authors have responded to the What next?: 
major compulsory revisions 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
none
Review for 10.1186/1471-230X-5-8 (2005)

Reviewer's report 
 The role of mast cells in the pathogenesis of pain in chronic pancreatitis Title: 
 1  26 October 2004 Version: Date: 
 markus w bÃ¼chler Reviewer: 
Reviewer's report: 
Title: The role of mast cell in the pathogenesis of pain in chronic pancreatitis 
Specific Comment: 
Willemijntie A Hoogerwerf and colleagues reported in this manuscript about the role of mast cells in 
pain pathogenesis in chronic pancreatitis. The Authors addressed with the present paper a very 
interesting and original topic. They concluded that the number of mast cells is increased in the 
pancreatic autopsy specimens from patients with chronic pancreatitis. They proved the “human” data 
in a TNBS animal model of chronic pancreatitis. The manuscript is well written and to our opinion 
requires minor changes. 
There different minor comments as follow: 
1. The Authors used for the study human tissue from autopsy specimens. The vitality or better the 
immunoreactivity of the tissue must be proved. In fact, it’s well known that autopsy specimens can react in a different way according to autolysis phenomena. 2. It would be important to obtain a pain score from the patients and correlate it with the tissue 
findings to investigate possible relationship between must cell infiltration and clinical data in human 
tissue (VAS scale) 3. The Authors must consider to add a group of patients undergoing surgery because of chronic painful pancreatitis to obtain fresh tissue specimens. 
4. The Authors must include a table where they specify how many hours after dead the tissue 
specimens were processed for the experiments. 5. Concerning the animal experiments, it must be clear when the animals were sacrificed after the induction of pancreatitis: i.e. 7 day, 14 day. 
6. The discussion is sometimes too speculative, in the reality we do not know whether mast cell 
degranulation induce pain or neurothophins induce pain and mast cell degranulation. To the reviewer 
opinion this argument must be clearly stated. 
 Accept after minor essential revisions What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review:
Review for 10.1186/1471-230X-5-8 (2005)

Reviewer's report 
 The role of mast cells in the pathogenesis of pain in chronic pancreatitis Title: 
 3  17 January 2005 Version: Date: 
 fred S gorelick Reviewer: 
Reviewer's report: 
General 
------------------------------------------------------------------------------- 
Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
------------------------------------------------------------------------------- 
Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
Figure 2 - provide a much higher magnification image of a mast cell (just a couple that are preferable 
adjacent to a non-mast cell - the magnification shown here would still be almost impossible for a 
reader to interpret 
The cartoon is not a high quality image and should be professionally redrawn. 
------------------------------------------------------------------------------- Discretionary Revisions (which the author can choose to ignore) 
 Accept after minor essential revisions What next?: 
 An article of importance in its field Level of interest: 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare that I have no competing interests
Review for 10.1186/1471-230X-5-8 (2005)

Reviewer's report 
 The role of mast cells in the pathogenesis of pain in chronic pancreatitis Title: 
 3  27 January 2005 Version: Date: 
 markus w bÃ¼chler Reviewer: 
Reviewer's report: 
General 
------------------------------------------------------------------------------- 
Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
------------------------------------------------------------------------------- 
Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) 
 Accept without revision What next?:
Review for 10.1186/1471-230X-5-8 (2005)

Reviewer's report 
 The role of mast cells in the pathogenesis of pain in chronic pancreatitis Title: 
 3  1 February 2005 Version: Date: 
 Kimberly Kirkwood Reviewer: 
Reviewer's report: 
General 
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Major Compulsory Revisions (that the author must respond to before a decision on publication can be reached) 
Response to 1. Argument is invalid. The authors purport to use the results of the present study to 
validate the distinction between experimental groups, which is not a valid means of stratifying the groups. The differences in mast cell counts between groups could be attributable to many other 
factors in this small number of patients besides the presence or absence of "pain" in the medical 
record at the time of autopsy. It is an interesting observation which may be worthy of investigation. 
Response to 2. Argument is simply a re-statement and adds nothing new. The fact remains that the 
technique used to measure pain has not been validated in this model of pancreatitis in this animal. 
The authors refer to a paper by Vera-Portocarrero et al in which this technique was supported by the use of opiods to block the response. Since Vera-Portocarrero's work used a different rodent (rat vs. mouse) and a different model of pancreatitis, it does not further their cause. The work would have 
been strenghtened by a second pain endpoint. 
Response to 3. fine. 
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Minor Essential Revisions (such as missing labels on figures, or the wrong use of a term, which the author can be trusted to correct) Responses are fine. 
------------------------------------------------------------------------------- 
Discretionary Revisions (which the author can choose to ignore) 
 Accept without revision What next?: 
 An article whose findings are important to those with closely related research Level of interest: 
interests 
 Acceptable Quality of written English: 
 No Statistical review: 
Declaration of competing interests: 
I declare i have no competing interests.