The FIB-4 Index Predicts the Development of Liver-Related Events, Extrahepatic Cancers, and Coronary Vascular Disease in Patients with NAFLD

Round 1

Reviewer 1 Report

In this manuscript, the authors report about an observational studies on the natural history of biopsy-proven NAFLD patients in Japan. Particularly, the authors tried to associate levels of fibrosis (evaluated through FIB-4) with the incidence of several conditions, both liver and non-liver related.

The manuscript is overall interesting. Several studies are currently aiming at investigating the natural history of NAFLD patients. Two remarks should be made: 1) in this study, NAFLD was ascertained through biopsy (and this is a strength of this manuscript, clearly); 2) the sample size of this study was low (and this is instead a weakness).

There are several other issues. In details:

 1) In the introduction, I suggest the authors to expand further on the relationship between NAFLD and CVD. Particularly, given that they looked at MACE (defined as CAD, stroke, and heart failure), the relationship between NAFLD and these three disease should be reported more clearly. A recent meta-analysis (https://pubmed.ncbi.nlm.nih.gov/34939092/) evaluated the association between NAFLD and the risk of these three conditions (and also AF); I think this should be referenced and discussed, along with other potential works. This is particularly important to give the reader the right context to interpret the current results.

2) Again, I have to say that the biopsy-proven diagnosis of NAFLD is clearly a strength point here. One should wonder why the authors were then interested into FIB-4, and why they did not analyse fibrosis according to the biopsy-ascertained levels of fibrosis. May the authors want to comment on this?

3) There are some methodological issues. First, 153 patients were excluded becaused not followed up for more than 100 days. To me, this seems illogical. If these patients died before 100 days, why not including them in the analysis? This can clearly have introduced a significant bias in the analysis. If these were lost at follow-up, again, this is a critical limitation of the study that should be acknowledged and discussed more. We need more information on these patients, regarding their baseline characteristics and what occurred to them. This is a crucial point.

4) The authors have stratified their patients according to median levels of FIB-4. There is plenty of literature that recommend to avoid the categorisation of continuous variables (like the FIB-4) since this could lead to misleading results (see for example: https://bmcmedresmethodol.biomedcentral.com/articles/10.1186/1471-2288-12-21). Clearly, here it would be more appropriate to use non-linear regression (for example with restricted cubic spline) to model the relationship between FIB-4 and the risk of outcomes. Can the authors comment on this, and perhaps modify their analysis accordingly?

5) Please report full p-values, avoid to report "p<0.05" or "n.s." both in tables and the text of the manuscript.

6) Given the long follow-up time, the rate of event is very low, for all the events analysed. This is concerning, since it is unclear why these patients had a so low incidence of adverse events. One reason may be the relative young age of the individuals included; but to me, it may suggest that there was a significant issue with loss at follow-up (i.e. drop-out, on which we do not have any information reported right now). The authors should report 1) how many patients were lost at follow-up (and therefore censored before the end of follow-up); 2) the number at risk under the kaplan-meier curves included in the figures of the manuscript. This is important to understand whether attrition bias was a significant concern here.

7) lines 194-195 (page 5) - this sentence seems odd and should be rewritten for improve clarity. Relatedly, the authors used several times the term "decompression" - what does it means? May the authors intend "decompensation"? If so, please replace and correct in all instances, also to improve consistency.

8) Table 2 - please report also number of events, and 95%CI for the incidence rates observed, for both groups. Obviously, comment #5 apply also here (and in the other part of the manuscript.

9) Probably, given the low sample size, the analysis on the ROC curves is the less interesting ones and may be dropped by the article. I think that there is very little value, given that uncertanity of the estimate are very high, since sample size and number of events were very low.

Author Response

Response to the comments of reviewers

We thank the editor and reviewers for the positive assessment of our manuscript and for identifying areas that required corrections and/or modification. The red-colored text in the revised manuscript is the corrected/modified text. All line numbers mentioned in each response to each comment refer to the small-size numbers that appear on the right margin of the text of the revised manuscript.

 

Reviewer 1

Comments and Suggestions for Authors

In this manuscript, the authors report about an observational studies on the natural history of biopsy-proven NAFLD patients in Japan. Particularly, the authors tried to associate levels of fibrosis (evaluated through FIB-4) with the incidence of several conditions, both liver and non-liver related.

The manuscript is overall interesting. Several studies are currently aiming at investigating the natural history of NAFLD patients. Two remarks should be made: 1) in this study, NAFLD was ascertained through biopsy (and this is a strength of this manuscript, clearly); 2) the sample size of this study was low (and this is instead a weakness).

There are several other issues. In details:

• In the introduction, I suggest the authors to expand further on the relationship between NAFLD and CVD. Particularly, given that they looked at MACE (defined as CAD, stroke, and heart failure), the relationship between NAFLD and these three disease should be reported more clearly. A recent meta-analysis (https://pubmed.ncbi.nlm.nih.gov/34939092/) evaluated the association between NAFLD and the risk of these three conditions (and also AF); I think this should be referenced and discussed, along with other potential works. This is particularly important to give the reader the right context to interpret the current results.

Thank you for the reviewer’s valuable comments. According to the reviewer’s comments, we added some descriptions and new references in the introduction of our revised manuscript (line 76-9).

• Again, I have to say that the biopsy-proven diagnosis of NAFLD is clearly a strength point here. One should wonder why the authors were then interested into FIB-4, and why they did not analyse fibrosis according to the biopsy-ascertained levels of fibrosis. May the authors want to comment on this?

Thank you for the reviewer’s critical comments. We fully agreed to your comments. In this study, we evaluated the ability of FIB-4 index as one of the most reliable and useful NITs to predict NAFLD prognosis in our cohort. We added some descriptions in our revised manuscript (line 84-5, 88-9).

• There are some methodological issues. First, 153 patients were excluded becaused not followed up for more than 100 days. To me, this seems illogical. If these patients died before 100 days, why not including them in the analysis? This can clearly have introduced a significant bias in the analysis. If these were lost at follow-up, again, this is a critical limitation of the study that should be acknowledged and discussed more. We need more information on these patients, regarding their baseline characteristics and what occurred to them. This is a crucial point.

Thank you for the reviewer’s important comments. To follow-up the prognosis of patients, we selected our study subjects who could be purchased more than 100 days in this study. Patients who were not followed up for more than 100 days did not have a second or subsequent outpatient visit. Therefore, we excluded 153 patients in this study. We added some descriptions in our manuscript (line 103-4, 151-2).

• The authors have stratified their patients according to median levels of FIB-4. There is plenty of literature that recommend to avoid the categorisation of continuous variables (like the FIB-4) since this could lead to misleading results (see for example: https://bmcmedresmethodol.biomedcentral.com/articles/10.1186/1471-2288-12-21). Clearly, here it would be more appropriate to use non-linear regression (for example with restricted cubic spline) to model the relationship between FIB-4 and the risk of outcomes. Can the authors comment on this, and perhaps modify their analysis accordingly?

Thank you for the reviewer’s critical comments. We think this is a very important comment. Due to technical difficulties, a spline curve analysis could not be performed in this study. Since the cohort size was a small in our study, the study was divided into two groups based on the median value. We would like to conduct a study using spline curves on a larger cohort in a future study.

• Please report full p-values, avoid to report "p<0.05" or "n.s." both in tables and the text of the manuscript.

Thank you for the reviewer’s comments. According to the reviewer’s comments, we described precise p-values in our revised manuscript (Table 1, 2, 3).

• Given the long follow-up time, the rate of event is very low, for all the events analysed. This is concerning, since it is unclear why these patients had a so low incidence of adverse events. One reason may be the relative young age of the individuals included; but to me, it may suggest that there was a significant issue with loss at follow-up (i.e. drop-out, on which we do not have any information reported right now). The authors should report 1) how many patients were lost at follow-up (and therefore censored before the end of follow-up); 2) the number at risk under the kaplan-meier curves included in the figures of the manuscript. This is important to understand whether attrition bias was a significant concern here.

Thank you for the reviewer’s important comments. We also think the information should be important for the readers. According to the reviewer’s comments, we added the number at risk under the Kaplan-Meier curves in the figures of our revised manuscript (Figure 2, 4).

• lines 194-195 (page 5) - this sentence seems odd and should be rewritten for improve clarity. Relatedly, the authors used several times the term "decompression" - what does it means? May the authors intend "decompensation"? If so, please replace and correct in all instances, also to improve consistency.

Thank you for the reviewer’s identification. We corrected these typos (line 188, 205, 233) and descriptions (line 197-8).

• Table 2 - please report also number of events, and 95%CI for the incidence rates observed, for both groups. Obviously, comment #5 apply also here (and in the other part of the manuscript.

Thank you for the reviewer’s fruitful comments. According to the reviewer’s comments, we added number of events, odds ratio, and 95% CI for the incidence rates in our study (Table 2). These descriptions should help the reader understanding.

• Probably, given the low sample size, the analysis on the ROC curves is the less interesting ones and may be dropped by the article. I think that there is very little value, given that uncertanity of the estimate are very high, since sample size and number of events were very low.

As the reviewer demonstrated, the number of events in the present study is small, but we presented it to show that the cutoff values are different among LRE, other organ cancer, and MACE. We would like to study the differences from the present cutoff values in the future by a larger study (line 334-5).

Author Response File: Author Response.docx

Reviewer 2 Report

1.Line 136: "Decompensation was defined as cirrhosis of the liver." I think the definition is not appropriate. 

2.Table 1: BMI at FIB4 Hi group: 27/0±4.6 should be 27.0±4.6, T-chol: 205/4±38.6 should be 205.4±38.6

Author Response

Response to the comments of reviewers

We thank the editor and reviewers for the positive assessment of our manuscript and for identifying areas that required corrections and/or modification. The red-colored text in the revised manuscript is the corrected/modified text. All line numbers mentioned in each response to each comment refer to the small-size numbers that appear on the right margin of the text of the revised manuscript.

 

Reviewer 2

 

フォームの始まり

Comments and Suggestions for Authors

1. Line 136: "Decompensation was defined as cirrhosis of the liver." I think the definition is not appropriate. 

We modified the descriptions in our revised manuscript (line 124-5). Thank you.

2. Table 1: BMI at FIB4 Hi group: 27/0±4.6 should be 27.0±4.6, T-chol: 205/4±38.6 should be 205.4±38.6

Thank you for the reviewer’s identification, and we apologize for our typos. We corrected the typos (Table 1).

Author Response File: Author Response.docx

Round 2

Reviewer 1 Report

authors have sufficiently answered my previous comments. There are still some typos that needs to be fixed at a proof stage (see for example legend of figures c. Comparison of new bleeding gastroesophageal varices development according to FIB-4 index) what does "new bleeding gastroespophageal varices" means? Please fix.

I have no further comments