JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-025-03664-x (2025)

Title: Global prevalence of Fusobacterium nucleatum and Bacteroides fragilis in patients with
colorectal cancer: an overview of case reports/case series and meta-analysis of prevalence
studies
Version: 3 Date: 07 Jan 2025
Reviewer's report:
Thanks for the opportunity to re-review this manuscript titled “Global prevalence of
Fusobacterium nucleatum and Bacteroides fragilis in patients with colorectal cancer: an
overview of case reports/case series and meta-analysis of prevalence studies”. Thanks to the
authors for their great responses (in a, b and 1st part of c). Just a few more comments, as Egger’s/
Begg’s test reporting/interpretation weren’t satisfactory (in 2nd part of c and d).
1. Regarding Egger’s test, the authors should please state what level of p-value will be considered
as publication bias in the ‘meta-analysis part of the methods section’. This will facilitate a more
objective interpretation of the presented data.
2a. The authors’ interpretation fell short of the standard way of interpreting these data - please
interpret based on the p-value obtained as was stated  in the (methods) statistical analysis
approach (as in 1 above).
2b. A better interpretation will state how for instance the “observed asymmetry in the funnel
plot which indicates some publication bias
Or
Observed symmetry in the funnel plot which indicates no publication bias
is supported by the p-value of Egger’s test being so so value (in view of 2a above)”. Please check
previous publications on funnel plot reporting or otherwise please consult ‘Cochrane handbook’
on meta-analysis reporting.
Best wishes,
Dr Ralph Udeh
Review for 10.1186/s12876-025-03605-8 (2025)

Title: Ultrasound Radiomics-Based Logistic Regression Model for Fibrotic NASH
Version: 3 Date: 07 Dec 2024
Reviewer:  Anwar Ashraf Abouelnasr
Reviewer's report:
Dear Authors, please address the following points below
-The study employs an SD rat model; however, the extrapolation of the results to human
populations presents challenges due to inter-species differences. It is essential for the authors
to provide additional details regarding the translation of the model into human clinical practice.
Furthermore, a discussion concerning any planned or ongoing human studies aimed at model
validation would be advantageous.
-Were standardized protocols established for acquiring SWE measurements? Additionally, how
were issues related to image quality, such as poor signals or noise, addressed effectively?
-What is the feasibility of implementing this technology within ultrasound systems currently
utilized in clinical settings? Are there any considerations regarding the computational
requirements necessary for radiomics feature extraction and analysis?
-Expanding the study to incorporate human data, either through retrospective analyses of clinical
ultrasound images or through a pilot clinical study, would be beneficial. This approach would
assist in evaluating the generalizability of the model and provide a more concrete foundation
for its clinical application.
-As highlighted in the discussion, the reliance on an animal model (SD rats) imposes limitations
on the generalizability of the findings to human patients. Although the rat model replicates
certain aspects of NASH progression, it cannot fully mimic human liver disease, especially
concerning the complexity and diversity inherent in NAFLD progression.
-Conducting research at a single medical facility may restrict the external validity of the findings.
A multi-center study, which includes data from a variety of institutions, would yield stronger
evidence concerning the generalizability and real-world applicability of the model. Additionally,
incorporating data from different ultrasound machines and operators could assess the model's
robustness across varied clinical environments.
-While the study provides valuable insights into the dimensionality reduction process and
feature selection through LASSO, the specific radiomic features retained—such as GLCM,
GLDM, GLRLM, GLSZM, and NGTDM features—are not sufficiently explained regarding
their biological significance related to liver fibrosis. Providing further context on the association
between specific features and fibrotic NASH, as well as their correlation with liver pathology,
could enhance the interpretability and clinical utility of the model.
Review for 10.1186/s12876-025-03605-8 (2025)

Title: Ultrasound Radiomics-Based Logistic Regression Model for Fibrotic NASH
Version: 3 Date: 12 Dec 2024
Reviewer's report:
Thank you for your efforts in evaluating the crucial histopathological index, fibrosis, based on
artificial intelligence and radiomics features. The base of the manuscript is well structured, but it
consists of some grammatical errors and lacks in the structure that must be considered. Based on
the overall content of the manuscript, the following modifications can be considered to improve
the clarity of the effort.
1- The literature review is so weak, and it doesn’t provide a clear view of the previous works
on the subject of the machine learning approaches in fibrotic NASH and fibrosis pathological
index. Besides, the performance of the previous studies was not presented to compare
2- The novelty of the study is not clear and according to the introduction and the procedure of
the study, it is so weak to be reported in this journal.
3- The standard guideline of the preparation of the rat samples in their diets was not mentioned.
4- What is the reason of choosing the blood biomarkers? Describe it in detail.
5- The lack of the citation to the claims in the manuscript is obvious. For example, there is no
evidence for definition of “fibrotic NASH”. Review carefully the manuscript and modify it based
on the certified references. The restriction of the citation degrades crucially the importance of
the study.
6- The hyperparameters of configuring the approaches in radiomics algorithm must be described,
such as the step of the neighborhood, the angle of survey, the overall characteristics of each
approach, the overall number of the extracted features by radiomics, etc.
7- Describe in detail the LASSO technique, Z-score, nomogram, and rad-score to clarify the
mechanism of feature selection, along with their references.
8- The misplacement of the dataset description in section 3-1 confuses the reader. The Results
section must describe the findings, solely and any discussion should be place in the related part.
9-  The overall radiomics features by “pyradiomics” package are limited. What is your
mechanism for extracting 1288 texture features and what was your mechanism to overcome the
crucial of overfitting and keeping the generalization of the model? Describe in detail.
10- What is the mechanism of choosing LASSO technique for feature selection and what is the
performance by employing alternative approaches?
11- The borderline of fibrosis is in stage 1 and 2. What is your mechanism to distinguish between
then and choosing F2, as critical point of fibrotic NASH?
12- What is your guideline or expert team to define the gold standard of fibrosis index? Describe
in detail
13- The application of logistic regression model does not guarantee the appropriate performance
for final model. A comparison of the performance of this algorithm should be presented with
other applicable methods, such as Random Forest, LightGBM, SVM, XGBoost, AdaBoost, etc.
Review for 10.1186/s12876-025-03605-8 (2025)

Title: Ultrasound Radiomics-Based Logistic Regression Model for Fibrotic NASH
Version: 4 Date: 01 Jan 2025
Reviewer's report:
1. I agree with the observations of the previous reviewers that it is crucial to provide additional
details regarding the translation of the rat model to human subjects. Unfortunately, the revised
manuscript does not address this concern adequately. Furthermore, no retrospective analyses
of clinical ultrasound scans, as suggested by Reviewer #1, were included. These omissions
significantly weaken the manuscript and make it difficult to generalize the proposed model to
clinical practice.
2. In the subsection on Ultrasound Data Acquisition, the authors stated: "In the 2D-SWE mode,
the adjacent liver-kidney section is selected, and liver and kidney elasticity values are measured
to calculate the liver-to-kidney elasticity ratio." This approach is not commonly employed
in clinical practice. Could the authors clarify why they chose to use the "elasticity ratio" in
this context? Additionally, are there any references supporting the use of this ratio in clinical
settings? Upon reviewing reference #40 (Zhang et al.), it seems that the hepatic/renal ratio in
their study was derived from grayscale intensities rather than elasticity measurements. If the
authors intend to use the elasticity ratio, could they explain how the region of interest (ROI) is
placed in the kidney? Is there an established protocol or guideline for this measurement?
3. The Discussion section would benefit from further refinement in terms of logical flow. For
instance, in the first paragraph, the phrase "As of September 2019..." is used. Could the authors
clarify the rationale for citing PubMed research results specifically from September 2019? It
would be helpful to explain why this time frame was selected.
4. It is intriguing that the authors have included the SWE values, which are part of the Ultrasound
Data Acquisition, in the "clinical model" rather than the "radiomics model". The "radiomics
model", as described, was constructed solely based on B-mode ultrasound images. Could the
authors please clarify the rationale for this choice? Additionally, do the settings of the B-mode
ultrasound have any impact on the feature extraction and selection process? If so, how did the
authors account for or minimize this potential impact?
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 4 Date: 01 Sep 2024
Reviewer's report:
This is an interesting article but with several limitations including the fact that alcohol -related
steatosis was not excluded, while other well-established serological tests were not evaluated in
the same cohort
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 4 Date: 06 Sep 2024
Reviewer's report:
The authors provide an intersting manuscript regarding the association between inflammation
and hepatic steatosis. The article is well-written and solid, however  have a few suggestions to
further improve it.
1. NAFLD should be substituted for MASLD according to latest nomenclature (ref: doi:
10.1097/HEP.0000000000000520)
2. The part regarding inflammation in introduction section ("Inflammation plays an important
role in the pathogenesis of NAFLD, which is not only a direct causative agent of
liver parenchymal cell injury, but also an important pathologic basis for driving disease
progression [16]. ") should be moved to the third paragraph (beginning with  "C-reactive
protein and lymphocyte ratio (CLR) have received much attention in recent years as an
emerging combination of inflammatory biomarkers") and further  expanded (with references
to mitochondrial dysfunction, endothelial cell dysfunction and gut dysbiosis and impaired
immune cells function), since inflammation plays a central role in presence and development
of MASLD (ref: doi: 10.1016/j.jhep.2017.11.014;  doi: 10.1053/j.gastro.2018.06.083;  doi:
10.3390/cells11162511; doi: 10.1002/hep.30506).  Alternatively, this section could be added in
discussion section, where the authors discuss inflammation.
3. Since inflammation sems to be critical not only for the presence of steatosis but also for the
development of  steathepatitis,  the authors should see if there was a connection between CLR
and non-invasive biomarkers like FIB-4 or APRI scores
4.  The findings should be better explained in the discussion section for those not familiar with
statistics. Was 1.08 the threshold for the presence of MASLD? If so, what was the positive and
negative predicitive value?
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 6 Date: 16 Sep 2024
Reviewer:  Maged Tharwat Elghannam
Reviewer's report:
The authors discuss the relation between MASLD and CLR and the possibility of its use as a
potential biomarker for identifying MASLD. MAFLD has a high prevalence all over the world
thanks to the increased prevalence of obesity and DM. It ranges from MAFLD to NASH to
liver cirrhosis up to HCC. Not all cases of NAFLD develop NASH or liver cirrhosis and its
complications.
Comments:
What are the reasons you chose the covariates?
What is the relation between CLR in a normal population? This represents a control for your
cases.
How can you use this CLR to differentiate between MAFLD and MASH?
I think it is mandatory to test this relationship before and after medications and compare this
with cap values before and after therapy.
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 6 Date: 19 Sep 2024
Reviewer:  Dimitrios S. Karagiannakis
Reviewer's report:
The authors presented a revised version of the manuscript that is better than the previous one.
All of my comments have been answered sufficiently. I have nothing more to add or mention.
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 7 Date: 25 Sep 2024
Reviewer:  Maged Tharwat Elghannam
Reviewer's report:
OK
Review for 10.1186/s12876-024-03458-7 (2024)

Title: Associations of C-reactive protein to lymphocyte ratio and  metabolic-dysfunction-
associated steatotic liver disease: evidence from NHANES 2017-2018
Version: 7 Date: 01 Oct 2024
Reviewer:  Dimitrios S. Karagiannakis
Reviewer's report:
I have nothing to add or mention. I believe that the manuscript is worth to be published.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 5 Date: 01 May 2024
Reviewer's report:
This work aimed to combine clinical trial data and real-word evidence using statistical
methodologies to predict long-term effectiveness of Darvadstrocel versus standard of care in
patients with complex Crohn’s perianal fistulas.
Major comments:
- Table 3: let median and IQR only. I'm not sure there's any point in leaving mean and median.
- The paragraph on the statistical model on page 12 (line 253) could be clearer. Its place in the
results section is unclear. The results section could begin by describing what the article aims to
study, and therefore the clinical outcomes.
- The fact that the data relating to the statistical model is mixed with the clinical data (line
285-292 for example) makes it difficult to read the manuscript (particularly for a clinician). A
section dedicated to the analysis of the models, separate from the clinical data, would perhaps
make it easier to read.
- The place of MSC versus SoC strategy in clinical practice in the light of these results could
be discussed.
Minor comments:
- Line 94: SoC/placebo
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 5 Date: 12 Jul 2024
Reviewer's report:
Thank you for the invitation to review the manuscript by Karki et al entitled " Predictive
modeling to evaluate long-term treatment effectiveness of darvadstrocel in patients with
complex perianal fistulas in Crohn’s disease”.
Treatment of CPF of CD is a challenge, there have been no major breakthroughs in recent years.
In this study, a comparative analysis of SoC vs DVS was performed in a statistical viewpoint
based on retrospective and RCT data and demonstrated that DVS was predicted to provide
greater long-term effectiveness than SoC.
The topic is interesting and emerging. The paper is well-written; however, the statistical
methodology is difficult to follow. Here are some comments that suggested to be clarified in a
revised version of the manuscript:
- In the Background section, the superiority of anti-TNFs may be highlight in contrast with
antibiotics or immunomodulators (ECCO guideline suggest against). Reference 4. may be
upgraded by 2024 releases.
- In the Background/Discussion section, preliminary results of ADMIRE-II may be commented.
- A high proportion of missing data of PDAI data from the PREFACE study was set as cause of
bias, please complete the manuscript with the ratios of missing data.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 5 Date: 16 Jul 2024
Reviewer's report:
The paper by Karki and co-workers has been meticulously prepared, the manuscript is well
written and the methodology  seems to be correct for me.
no major points:
minor points:
Following points should be considered:
line 39-42:  you found a difference between the groups which was described as  longer or a
higher estimated proportion of patients,. How significant is this difference? Is there the option
for a calculation (p) of this difference in your model?
Line 80: Meanwhile the American data of DVS have been published as an abstract. The
American data are somewhat contradictory to the European. So far we don't know why we find
this difference. I recommend however , to briefly mention and discuss these new data in the
introduction and in the discussion
332 . is missing
371; I don't think you should consider fistular diseaase as a rare disease.
325
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 5 Date: 19 Jul 2024
Reviewer:  Claire Liefferinckx
Reviewer's report:
Abstract:
About method part:
• More details should be given about the approach of predictive models instead of developing
which countries were involved in the three studies.
About result part:
• p-value should be added for proportions
About the conclusion:
• this conclusion is not useful and should be rephrased to capture the key results of the study
instead of rephrasing the aim of the study.
Background
• There is no “.” to separate the sentences. Syntax should be improved
• The reason for using such predictive models should be mentioned since introduction to help
the reader to understand the added value of this methodology.
Methods
• Patients from the three studies (ADMIRE-CD, INSPECT, and PREFACE) are different or
some patients could be present in the studies? If risk of duplicated data, how it was managed?
• Clinical validation of the model: this is a good idea to have an external validation of the model
before implementing. Nevertheless, I’m not convinced that clinical experts are the best experts
to properly evaluate the structure, assumptions, and inputs of the semi-Markov model
Results/ Discussion
• Table 3 should include comparative analyses (with p-val) between ADMIRE-CD and
PREFACE
• Regarding the following sentence: “The best-fitting location- and shape-adjusted models
decreased the differential treatment effect for all definitions of relapse when compared with the
Gompertz curve, which was chosen as the base-case model because its estimates were considered
appropriate and clinically plausible by the panel of clinical experts”. Authors should develop
what means “clinically plausible”
• It appears unclear how authors managed the differences between cohorts (specially between
ADMIRE-CD and PREFACE) before pooling them together.
• There is no external validation of the predictive model. This might be explained, as mentioned
by the authors, be the low number of events (particularly relapses) which limits the ability to
split the dataset for external validation. Nevertheless, this should be mentioned in the limits.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 8 Date: 07 Sep 2024
Reviewer's report:
A very relevant study aiming to clarify the long-term effectiveness of DVS against SoC, through
predictive modelling.
Disclosure: I reviewed a manuscript that had been previously reviewed by 5 reviewers, with
adequate replying from the authors.
Hence, I will present some comments, mostly (but not only) related to easiness of reading of
the text.
- P11,L235 – Table 2 – I would suggest that DVS and PBO/SoC would figure in a left column
so that the number of pts in each treatment could be summed in a total column on the right side
of the table. This would help understand the pts populations as studies are to be merged.
- P12,L254 A short sentence on the most relevant differences between groups would help the
reader – for example, almost half of the pts in PREFACE had luminal active disease, which
contrasts to the ADMIRE pts.
- P12,L257 I agree with Rev.#1 that median, IQR would be preferable. However, authors replied
that p-value was calculated using mean, SD. Nevertheless, I think that presenting both in the
table makes it more difficult to read, so maybe one of these distribution measures could figure
in the caption below the table.
- P13,L265-266 – I cannot fully understand what authors mean or wish to convey, when they
state that patients that present both “less remission and relapse” are “more stable patients”…
Less remission rates, means more activity; less relapse rates, means more stability of remission.
Moreover, as previously stated, PREFACE pts have active luminal CD in almost half of the
patients. So, authors should explain better what they want the reader to learn from this data. The
same for the discussions section, P17, L364.
- P14, L295 – “shorter estimated time to CPC remission…” – shouldn´t this be “longer”?
- P15,L307-308 – Fig.3C and 3D display different long results; this should be addressed in the
text.
- FIG.3 – As 3A and 3B are related to time to remission and 3C and 3D are related to time to
relapse, I suggest their separation (e.g. 3C + 3D should be FIG. 4A. and 4B); as it is, the reader
may tend to compare FIG. 3A and 3B with 3C based on their visual similarity, which, of course,
makes no sense.
- P.17,L365 – Not sure if the ADMIRE-CD pts are really more refractory pts, in what PCF
is concern. They have more duration of disease and more immunosuppressive/biologic use
but they have achieved luminal remission, while a part of the other studies’ pts have not. If
a pt is refractory to IS/biologics both in luminal- and PCF-CD, can he be considered more
refractory? Of course this would depend on the previous treatments and other variables…so I
am not comfortable with this sentence.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 8 Date: 07 Sep 2024
Reviewer's report:
Dear Authors,
Thank you for considering and addressing my comments in your revised manuscript. I am happy
with the latest version of your paper thus I have no further comments.
Once again congratulations on your work.
Best wishes
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 8 Date: 14 Sep 2024
Reviewer:  Claire Liefferinckx
Reviewer's report:
I have no more comments. Authors appropriately answered  to questions.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 8 Date: 15 Sep 2024
Reviewer's report:
The authors answered all questions and changed the manuscrpt. I have no fuether remarks
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 8 Date: 15 Sep 2024
Reviewer's report:
Dear authors,
I would like to congratulate you on this nice manuscript that comprehensively outlines the used
complex methodology  to show long-term beneficial effects of DVS compared to standard of
care based on RWE from the ADMIRE-CD, INSPECT and PREFACE study.
Nonetheless, I would like to make some remarks/suggestions:
Introduction section:
-  Page 3 line 60-61: apart from infliximab other advanced medical treatment options have shown
good potential in subgroup analyses from RCT’s. Furthermore, there are currently dedicated
studies ongoing to evaluated efficacy of guselkumab (FUZION study) and ustekinumab (USTAP
study) compared to placebo in treatment of PFCD.
- Page 4 line 81-83 section on ADMIRE-CD: please add data and/or comments on the recent
result of ADMIRE-CD II
Methodology section:
- did you consider to add data from the ADMIRE-CD II trial and/or the INSPIRE registry?
- it might be good to specify what is meant with "standard of care" (in the PREFACE study)
- could you comment on why you did not use the same endpoints as the ones used in the
ADMIRE/INSPECT?
Results section:
- I would suggest to add numbers and p-values to  the findings described in the text
Discussion section:
- please provide some comments on cost-effectiveness of DVS compared to SoC, particularly
in light of the findings of ADMIRE-CD II
As a general minor comment, I would suggest to use the abbreviation PFCD to describe perianal
fistulising Crohn's disease, as I feel this is more commonly used in literature.
Best wishes
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 9 Date: 18 Oct 2024
Reviewer's report:
The authors correctly addressed all questions. I have no further comments- Congratulations on
your work.
Review for 10.1186/s12876-024-03513-3 (2024)

Title: Predictive modeling to evaluate long-term treatment effectiveness of darvadstrocel in
patients with complex perianal fistulas in Crohn’s disease
Version: 9 Date: 20 Oct 2024
Reviewer's report:
Dear authors,
My comments and questions were addressed appropriately. I have no further remarks.
Best wishes
Review for 10.1186/s12876-024-03577-1 (2024)

Title: Superior Persistence of Ustekinumab Compared to Anti-TNF in Vedolizumab-
Experienced Inflammatory Bowel Diseases Patients: A Real- world Cohort Study
Version: 1 Date: 27 Sep 2024
Reviewer's report:
Thank you for the invitation to review the manuscript by Horng-Yih Chiu et al entitled " Superior
Persistence of Ustekinumab Compared to Anti-TNF in Vedolizumab-Experienced Inflammatory
Bowel Diseases Patients: A Real-world Cohort Study”.
Horng-Yih Chiu et al performed a retrospective analysis on the persistence of UST vs anti-TNF
amongst IBD patients after VDZ failure. The topic is interesting. The paper is well-written, here
are some comments that suggested to be clarified in a revised version of the manuscript:
• Were other anti-TNF agents (golimumab, certolizumab) used?
• Please define catastrophic illness in Methods
• Was IFX dose escalation (to 10 mg pro kg) allowed?
• How was uni- and multivariable (multivariate?) models handled? Please specify model
selection.
• The high persistence rate of UST is interesting but needs explanation. Why was IFX dose
escalation rate lower than UST while the persistence was higher? Were these cases due to allergy
or PNR or something else? You state that the most frequent cause of failure was secondary loss
of response. Please comment.
• Is it available to use VDZ as first line in general in your center? If yes, please comment it, if no
please describe patient population in more details regarding comorbidities and other influencing
factors.
• I suggest comparing UST persistence rates of other second line use (PMID: 32441396,
36600684, 32249966) near the first line use in the Discussion.
• Please add limitations of the study.
• Please comment on the weakness of persistence outcome compared to other (harder) efficacy
outcomes (chronic mild activity, treatment supplementation).
• The label of Y axis of Figure 1,2,3 may be changed to probability of failure.
Review for 10.1186/s12876-024-03577-1 (2024)

Title: Superior Persistence of Ustekinumab Compared to Anti-TNF in Vedolizumab-
Experienced Inflammatory Bowel Diseases Patients: A Real- world Cohort Study
Version: 1 Date: 03 Dec 2024
Reviewer's report:
The authors compared the persistence of UST and anti-TNF therapies in IBD patients who were
previously exposed to VDZ. There are two major limitations in this study:
1. Lack of effectiveness outcomes: The study does not report key effectiveness outcomes, such as
endoscopic or clinical responses. While therapy persistence is an important measure, it does not
provide a complete picture of the therapy's benefit without evaluating these additional outcomes.
2. Dose escalation and bias in persistence: UST was associated with longer therapy persistence
in this study. However, UST-treated patients also had higher rates of dose escalation. Since it is
well-known that dose escalation can improve outcomes and persistence, it is possible that anti-
TNF-treated patients were not given the same opportunity for dose escalation as UST-treated
patients. The manuscript does not clarify the criteria for dose escalation or whether anti-TNF
serum levels and antibodies were measured. Patients might have developed immunogenicity and
required higher dosing or the addition of immunomodulators, but this information is missing.
Additional remarks for the authors to consider:
Methods:
• Were these patients exclusively exposed to VDZ prior to starting UST or anti-TNF therapy?
If so, this should be explicitly stated in the manuscript.
• What were the exclusion criteria? How many patients were excluded based on each criterion?
• Were the screened patients included consecutively?
• I strongly recommend following the STROBE checklist and including a completed version
with the revised submission.
• The Methods section should be reorganized into subsections, such as: Cohort, Collected
Variables, Outcomes, Statistics, etc.
• To identify predictors of 52-week treatment persistence, Cox proportional hazards models
should be used instead of logistic regression, as the outcome is “time to event.”
• How were cases handled where patients experienced flares requiring hospitalization and
received intravenous steroids or other therapies but continued their index therapy (UST or anti-
TNF)? Similarly, how were cases managed where patients underwent surgery but maintained
their index therapy? Were these situations considered therapy persistence, and were such cases
recorded?
Results:
There appears to be a coding or statistical error in the reported hazard ratios (HR). The
manuscript states that UST exhibited longer persistence in the overall IBD cohort as well as in
the CD and UC sub-cohorts. However, the reported HR values are >1, which is incorrect.
• An HR >1 indicates an increased hazard for the undesirable outcome (therapy discontinuation),
which contradicts the claim that UST is associated with longer persistence.
• If UST was indeed associated with longer persistence, the HR values should fall between 0
and 1. Any values outside this range suggest a coding or calculation error.
Review for 10.1186/s12876-024-03559-3 (2024)

Title: Health-care resource use and costs associated with inflammatory bowel disease in
northwest London: a retrospective linked database study
Version: 0 Date: 09 Nov 2024
Reviewer's report:
This is an interesting article which highlights aspects of the cost of IBD not previously reported
from the UK. By analyzing real data, the authors avoid the speculation of cost-modelling in
previous UK publications.
The data are well presented overall.
I would suggest more attention to the following issues:
Page 3: "Biosimilars are 70% less expensive." Is this really true in the UK?
Disease definition in a database: Please related to the possibility of error of diagnosis. Also, did
the authors check for a change of diagnosis?
I did not understand the statement that half were diagnosed 2 years or longer (page 6). What was
the requirement for inclusion. Was a single record in the database sufficient?
Unlike other publications, the percentage of persons in remission is very high. How is this
possible?
The cohort of UC was essentially composed of older people, unlike CT or undefined. Please
comment.
In 50% the ethnicity was unknown. Please comment.
Smoking was not reported. Is this not part of the NHS database?
Time since diagnosis was not given (or did I miss this?).
The cost per patient data: Is this per year? Per period?
The labelling should be consistent in all the graphs.  The reader cannot be expected to refer to
previous graphs to understand all items.
References: These are obviously the prerogative of the authors. However, I would like to point
out that ref. 38 refers to children. Furthermore, the authors' work would be more relevant if
it were compared with the landmark studies of other groups reported in the literature, such as
Burisch et al. in Lancet Gastroenterology Hepatology 2020 and2023.
Review for 10.1186/s12876-024-03559-3 (2024)

Title: Health-care resource use and costs associated with inflammatory bowel disease in
northwest London: a retrospective linked database study
Version: 0 Date: 09 Nov 2024
Reviewer:  Panagiotis Tsibouris
Reviewer's report:
Authors try to estimate direct costs of IBD Usually indirect costs like lost of productivity,
DALYs, obligatory leaves from work to transfer patients unable to be self supported, increase of
anxiety and depressive mood etc represent the bottom of the iceberg For those cost authors have
to give a hint since they have selected to talk about the top of the iceberg An interesting point
is only 5% of patients were initially treated with biologics Thus the percentage of patients with
early remission was very low Abstract The first sentence has little to do with IBD economics
and should be replaced with something closer to the theme More data could be presented apart
from a general overview for active disease Methods  Statistics Was there a need for advance
statistics to asimilate costs taking into consideration various comorbidities, disease activity and
demographics? Results Multivariated analysis would be more effective to define risk factors for
non-elective treatment or use of biologics The same might be valid for increase expenses
Review for 10.1186/s12876-024-03576-2 (2024)

Title: Human blood metabolites and gastric cancer: a Mendelian Randomization Analysis
Version: 0 Date: 10 Jul 2024
Reviewer's report:
Major comments
1. [Introduction] I suggest an additional explanation of previous epidemiological studies on
associations between metabolites and cancer or gastric diseases. I noticed that the author
described the previous studies in the Discussion section, and I suggest that the author move the
part of the contents to the Introduction section.
2. [Introduction] It would be better if the author stated the specific SNPs or genes linked with
serum metabolites identified by previously published studies.
3. [Results: Replication and Meta-analysis] According to TableA5, only three (not seven)
metabolites seem to show concordant direction in discovery and replication.
4. [Discussion] I suggest describing the biological functions and clinical implications of the
three metabolites identified.
Minor comments
1. [Abstract] In the conclusion section, I suggest to mention specific metabolites (e.g., 3-
methyl-2-oxovalerate, piperine, phenylalanylphenylalanine).
2. [Introduction] There are some unnecessary spaces between paragraphs.
3. [Materials and Methods: GWAS Data for Human Blood Metabolites] The Shin’s study needs
citation.
4. [Results: Strength of the IVs] The way to mention the supplementary table differs between
the manuscript and the additional table file (e.g., Manuscript: Table A2, Supplementary table
file: Table S2).
Review for 10.1186/s12876-024-03576-2 (2024)

Title: Human blood metabolites and gastric cancer: a Mendelian Randomization Analysis
Version: 0 Date: 14 Sep 2024
Reviewer's report:
Thank you for inviting me to review this paper. The study investigates the causal relationship
between blood metabolites and the development of stomach cancer, using Mendelian
randomization analysis to infer these effects through genetic variation. Here are my review
comments:
1.Structure:he introduction is thorough but could benefit from simplification for clarity. Some
sentences are repetitive; rephrasing them to avoid redundancy will help readers better grasp the
author's message.
2.Research Design:To make the research design more accessible to a broader audience, consider
simplifying complex methodological terms. Breaking down the three hypotheses of Mendelian
randomization into more straightforward language or using footnotes for additional explanations
would be helpful.
3.Instrument Selection:The term "exclude palindromic SNPs with intermediate allele
frequencies such as A/T or G/C" may be unclear to readers without a genetics background.
Adding a brief explanation, such as: "Palindromic SNPs, where two alleles are indistinguishable
(e.g., A/T or G/C), were excluded to prevent analytical ambiguity," could clarify this concept.
4.Discussion:The phrase "In recent times the worldwide prevalence of GC has seen a rise" could
be revised for formality and precision. I recommend: "The global incidence of stomach cancer
has increased in recent years, highlighting the need for early screening and preventive measures."
The statement "To date, only a few studies have delved into the role of circulating 3-methyl-2-
oxyvalerate in tumorigenesis..." would be strengthened by including additional references on
the specific role of 3-methyl-2-oxyvalerate. Incorporating more studies could reinforce this
argument.
5.Charts:Ensure that all chart legends are clear and descriptive, particularly for complex visual
data such as forest plots and meta-analyses. This will aid readers in accurately interpreting the
data.
Overall, this study offers valuable insights into the molecular mechanisms of gastric cancer and
provides a foundation for screening and intervention strategies using metabolites as potential
biomarkers. After addressing the suggested revisions, I believe the paper will be suitable for
publication. Therefore, I recommend it for publication pending comprehensive revision.
Review for 10.1186/s12876-024-03576-2 (2024)

Title: Human blood metabolites and gastric cancer: a Mendelian Randomization Analysis
Version: 0 Date: 05 Oct 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses a testable research
question(s) (brief or other article types: is there a clear objective)?
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with technical rigor to allow
confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
No - there are minor issues
OVERALL MANUSCRIPT POTENTIAL - Is the current version of this work technically
sound? If not, can revisions be made to make the work technically sound?
Probably - with minor revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: This is a review of a manuscript titled "Human blood metabolites
and gastric cancer: a Mendelian Randomization Analysis". In this analysis, authors show that
the genetic components predisposing individuals to elevated levels of 3-methyl-2-oxovalerate
and piperine also predispose to gastric cancer, while the genetics underpinning elevation in the
levels of phenylalanylphenylalanine  prove protection against the development of this malignant
disease. Manuscript is well written. The only problem that noticeable  is that the Intro part is very
short. May be the part that describes previous metabolic studies of GC could be moved to Intro
section. Also, please consider abbreviating phenylalanylphenylalanine to Phe-Phe dipeptide or
likewise, to make respective parts of MS more readable. I see no problems with  statistical
analysis performed.
On a side note, please make sure that the text editing software uses English system of the word
breaking between lines. In current version of MS, each transferred word is broken in random
place, rather than by syllables, which makes the text hard to read.
REQUESTED REVISIONS:
Please see the note about expanding Introduction part of this MS and other small notes above.
Otherwise, all good
ADDITIONAL REQUESTS/SUGGESTIONS:
please see above. This is MS of excellent writing quality.
Review for 10.1186/s12876-024-03576-2 (2024)

Title: Human blood metabolites and gastric cancer: a Mendelian Randomization Analysis
Version: 1 Date: 02 Dec 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: This is a repeat review of a manuscript titled "Human blood
metabolites and gastric cancer: a Mendelian Randomization Analysis"".
Study demonstrates show causal connections between the genetic components predisposing
individuals to elevated or lowered levels of certain blood metabolites predispose to gastric cancer
or provide protection against the development of this malignant disease.
Manuscript is well written, and much improved after revision.  I see no problems with  statistical
analysis performed.
two small things (not requiring re-reviewing)
1) Please abbreviate phenylalanylphenylalanine to Phe-Phe dipeptide in abstract as well.
2) Please make sure that the gene names (as opposed to proteins)are italicized according to
HUGO convention. For example, in the phrases "in the PPM1K gene", "In the FADS1 gene"
ADDITIONAL REQUESTS/SUGGESTIONS:
Please do small corrections noted above (does not require re-review)
Review for 10.1186/s12876-024-03576-2 (2024)

Title: Human blood metabolites and gastric cancer: a Mendelian Randomization Analysis
Version: 2 Date: 21 Dec 2024
Reviewer's report:
PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: This is repeat review of the manuscript "Human blood metabolites
and gastric cancer: a Mendelian Randomization Analysis"
The authors have revised all issues raised after initial submission in this revised manuscript. It
looks good now, and may be published
ADDITIONAL REQUESTS/SUGGESTIONS:
MS looks good now
Review for 10.1186/s12876-024-03570-8 (2024)

Title: Fatigue, pain and faecal incontinence in adult Inflammatory Bowel Disease patients and
the unmet need: a national cross-sectional survey
Version: 2 Date: 10 Oct 2024
Reviewer's report:
This is an interesting manuscript on an important topic.  Thank you for doing this work!
I have no major concerns regarding the soundness of the research and the results presented.  I
thought your discussion section, in particular, was well written and enjoyable to read.
Review for 10.1186/s12876-024-03570-8 (2024)

Title: Fatigue, pain and faecal incontinence in adult Inflammatory Bowel Disease patients and
the unmet need: a national cross-sectional survey
Version: 2 Date: 22 Oct 2024
Reviewer:  Amira A A Othman
Reviewer's report:
The researchers published the scientific results of this study in several journals. I do not see the
benefit of re-publishing even after making some changes in the form of presenting the results of
the scientific study because they will remain as they are.
https://assets-eu.researchsquare.com/files/rs-5027352/v1/6dfc977e-af52-4146-
a654-022a01659152.pdf?c=1729509718
https://gut.bmj.com/content/72/Suppl_2/A109.1
https://www.researchgate.net/
publication/371689656_P106_The_relationship_between_fatigue_pain_and_urgency_in_8486_people_with_inflammatory_bowel_disease_a_survey
file:///C:/Users/%D8%B9%D8%A8%D8%AF%D8%A7%D9%84%D8%B1%D8%AD
%D9%85%D9%86%20%D9%86%D8%B8%D9%8A%D9%85/Downloads/
DOP59_What_is_the_relationship_between_fatigue_pai.pdf
Review for 10.1186/s12876-024-03570-8 (2024)

Title: Fatigue, pain and faecal incontinence in adult Inflammatory Bowel Disease patients and
the unmet need: a national cross-sectional survey
Version: 2 Date: 01 Nov 2024
Reviewer's report:
This is a well intended study addressing as mentioned un met needs in the realm of IBD. The
manuscript did a great job in approaching a large cohort of patients and in obtaining a greater
sample size.
Some of comments on the study:
1. While addressing some of the key symptoms of fatigue, pain and fecal incontinence the  group
may have missed exploring other unmet features of loss of work,  socioeconomic impacts and
limitation to social life and so on.
2. While the presence or absence of the symptoms in past 7 days do provide with some insight
many of these patients do have prolonged disease with variable days of symptomatology
3. The scoring system used may work for pain but do not appear to be valid for fatigue or fecal
incontinence. This may  also shed doubts on correlation being concluded between these variables
4. As acknowledged this study is vary much affected by reporting bias
Overall the study sheds light on clinically relevant unmet needs in IBD and also on patients
requesting for aid for these issues.