Review Reports - Acquired Platelet Dysfunction with Eosinophilia: A Narrative Review

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The Authors present a paper: "Acquired platelet dysfunction with eosinophilia-the blind men's elephant: a narrative review" that honestly they add very little to what is already known in literature. Their literature research is appropriate but no conclusions have been reached.

Introduction is fine as well as Results but the tables are useless and difficult to follow.

I appreciate the effort of the Authors but their results are very poor and not helpful for the readers. The presence of eosinophilia and ITP is known and not well understood but benign in any case.

The take home message is missing

Author Response

Dear Editor-in-Chief,

Thank you for the kind instructions and the reviewers’ reports. The remarks and suggestions are extremely constructive. The manuscript has been revised accordingly. As the available evidence is limited by its overall quality, I understand that this review can only be exploratory. Over-zealous conceptual claims are therefore unwarranted. However, as a clinician who has been managing such cases, I can feel acquired platelet dysfunction with eosinophilia (APDE) as an orphan disease and no progress has been made throughout the years. A narrative review in a respectable journal would be a good start to call for changes. Extensive changes have been made. The following summarizes my responses to the Reviewers.

Reply to Reviewer 1

I thank the Reviewer for the general comments. I understand that to the well-educated scholars, the present review probably adds very little to their knowledge. But for the vast majority of practitioners, APDE is an obscure condition with no clear definition. At times, eosinophilia was thought to be a mandatory condition for diagnosis while thrombocytopenia was thought to be an exclusion criterion. This review has found otherwise.
I agree that the Tables 2, 3, and 4 are difficult to follow. Therefore, they have been moved to the Supplementary file. I am sorry for making the original manuscript so boring.
I agree the parts about eosinophilia and thrombocytopenia have not been written clearly. It has been re-written (Lines 249-251 and 302-305). Table 2 has been added to compare APDE with immune thrombocytopenia (Lines 312-313).
The Conclusions have been revised to include the take home message (Lines 361-372).

Reviewer 2 Report

Comments and Suggestions for Authors

I have several questions regarding the review that could help enhance the quality of the paper.

Do the authors suggest a set of specific diagnostic criteria (even provisional) of their findings or merely a description of variability.

What minimum role if any should eosinophilia play in diagnosis supportive optional or irrelevant.

Can the authors present a clearer PRISMA-style flow diagram and explicitly justify decisions to exclude, especially when dealing with large datasets such as Laosombat et al.

Are the authors able to elaborate on the possible mechanisms that could connect the dysfunction of platelets, eosinophilia, and immune processes and explain whether existing evidence is biased toward one hypothesis.

Which clinical or laboratory characteristics can be consistently used to distinguish between this condition and Immune thrombocytopenia in practice.

Are the authors able to suggest a feasible management and follow-up algorithm (e.g., how frequently to monitor, how to indicate platelet transfusion, what is the role of anti-helminthic therapy.

Author Response

Dear Editor-in-Chief,

Reply to Reviewer 2

I am tempted to propose a set of diagnostic criteria as suggested by the Reviewer, but the evidence found does not permit such a conclusion. Nevertheless, a suggested approach to the diagnosis in the Conclusions has paved the way how a diagnosis of APDE can be made with tests that are commonly found in most institutions. (Lines 361-372)
The Reviewer’s reminder about the role of eosinophilia is important. A specific statement has been added accordingly (Lines 249-251).
A flow diagram (Figure 1) has been added according to the Reviewer’s suggestion (Line 124).
In response to the Reviewer’s query if there is a connection between platelet dysfunction, eosinophilia, and immune processes, the available evidence does not provide any solution. On the other hand, the morphological and thrombocytopathic similarities between APDE and hereditary grey platelet syndrome provide another clue. A recent study from a relatively large cohort of patients with grey platelet syndrome has expanded the clinical manifestations to include immune dysregulation and autoimmune disorders. The loss of the platelet granules and the GPS protein may be central in the pathogenesis. Changes in the manuscript have been made accordingly (Lines 275-276, 291-293).
In response to the Reviewer’s comment, Table 2 has been added to compare APDE with immune thrombocytopenia (Lines 312-313).
In response to the Reviewer’s queries, a suggested follow-up plan (Lines 329-331) and caution on the empirical use of anti-helminthic treatment (Lines 326-327) have been added. No changes are made with respect to the indication for platelet transfusion. The available evidence is not sufficient to permit any firm statements on this point.

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Author,

Thank you for the opportunity to review this interesting manuscript.

The manuscript addresses an interesting and clinically niche topic: acquired platelet dysfunction with eosinophilia (APDE), a rare condition that is poorly defined and insufficiently described in the literature. The current version of the manuscript requires some methodological, editorial, and interpretive revisions before it can be accepted for publication. Below are my detailed comments.

MAJOR CONCERNS

The author describes the study as a narrative review; however, its structure (searches in MEDLINE, EMBASE, and Google Scholar; inclusion and exclusion criteria; data extraction; aggregation of numerical results; and statistical analysis) is more consistent with a scoping review or a simplified systematic review. In its current form, the methodology falls somewhere between a narrative essay and a systematic review, which undermines the credibility of the results. The author should clearly decide whether this is a narrative review (in which case the pseudo-meta-analytic aggregations should be removed) or a full systematic/scoping review (in which case the methodology should be aligned with PRISMA standards).
The author compiles data from observational studies, case series, individual case reports, and conference abstracts.

He then presents combined numerical percentages, which may suggest a statistical precision that does not actually exist. Such figures should be treated solely as exploratory and not as epidemiologically representative estimates. The author should clearly state this and temper the language of his conclusions.
The author repeatedly claims that the term APDE is a “misnomer,” proposing new terms and describing “feedback loop failure.” It is an interesting hypothesis, but it is presented too categorically. Based on a review of the literature, one cannot propose a name change with such certainty. The conclusions should be tempered and presented as a proposal for discussion, rather than as a conclusion derived from the data.
The author suggests a possible link between APDE and ITP based on the presence of thrombocytopenia in some patients. This is an interesting hypothesis, but one that is currently poorly documented.
The author cites data without giving sufficient consideration to their analytical limitations. In particular, the bleeding time is now considered a historical test with poor reproducibility and limited diagnostic value. Some of the cited studies even date back to the 1970s! A separate section on the limitations of historical diagnostics is required.
A significant number of cases originate from individual centers in Thailand and Singapore. This may not reflect the actual epidemiological situation, but rather potential geographical and referral biases. The author mentions this issue but does not analyze it in sufficient depth. This is crucial for interpreting the phenomenon as a whole.

MINOR CONCERNS

Some of the expressions in the manuscript (e.g., “the blind men’s elephant”) are journalistic in tone and less appropriate for an academic paper. I recommend adopting a more neutral, academic style.
Before publication, professional proofreading is necessary to correct linguistic and stylistic errors. Some of the phrasing also sounds unnatural and is likely the result of calques.
Fisher's exact test was used for selected comparisons, but: no correction for multiple comparisons, no confidence intervals, no justification for exploratory analyses, and no information on the missing data strategy.
Tables 2–4 contain a vast amount of abbreviations and raw data. It might be worth considering moving some of this information to a supplement or shortening the main tables.
The recommendation to expedite diagnosis by assessing gray platelets in a smear is interesting but requires prospective validation. It should not be presented as a quasi-standard of care.
The author frequently uses individual case reports to support broader arguments (e.g., the geographical distribution of the disease, smear diagnosis, the absence of a link to parasites, the link to ITP).
There is no “Limitations” section as a separate chapter. With so many limitations, this topic deserves its own section.

Author Response

Dear Editor-in-Chief,

Reply to Reviewer 3

I appreciate the Reviewer’s comments and suggestions about the methodological approach. Due to limitations in human and technical resources, I am unable to carry out a full systematic or scoping review on this topic. However, I believe a more transparent way of literature search is still acceptable for a narrative review. To avoid the confusion with a systematic review, I have removed the large tables from the manuscript and put them into a supplementary file. Statistic computations are kept to a minimum and are just done in the text as a support to the discussion.
I appreciate the Reviewer’s instructions, especially the cautions on the over-interpretation from the pooled data. As suggested, the major and important limitations of the review are emphasized in the added section 5: Limitations (Lines 352-360). The exploratory nature of the review is highlighted. The potential bias when pooling data from a large number of case reports is raised. Change are also made in the Abstract (Lines 13-15).
The Reviewer is right to point out that renaming APDE requires much stronger justification. Therefore, I have removed the parts that suggest APDE as a misnomer and replaced them as a proposal for re-evaluation (Lines 24-30, 338).
The Reviewer’s comments about APDE and immune thrombocytopenia are valid. Table 2 has been added to highlight the similarities and differences between two conditions. (Lines 312-313)
I share with the Reviewer the frustration that bleeding time is still used in some pediatric centres. The test has been obsolete in most contemporary practices and I do not find it necessary in the management of APDE. Unfortunately, the test is deeply rooted in many Southeast Asian countries and is cited as the standard test for platelet function in the latest publication from Thailand in 2018. Hence, it is not possible to put up a separate section on the limitations of historical diagnostics as suggested. However, as the Reviewer has noticed, I have stated clearly in the manuscript that bleeding time is not a test to follow based on the reasons the Reviewer has mentioned (Lines 262-263). And in the Conclusions where diagnostic evaluation for suspected APDE is summarized, the use of bleeding time is not mentioned. (Lines 362-372)
The Reviewer’s comment that it could have been a referral bias when cases are concentrated in Thailand and Singapore is interesting. However, it is difficult to prove based on the review of the literature. It is also very unusual for an acquired haemological disorder to be so restricted to the paediatric population. The exceptional adult cases reported from “ancient” Singapore could have suggested that clinicians’ awareness and interest in APDE is a critical factor. When the awareness and interest is gone, mild and uncommon bleeding disorders such as APDE can be passed unnoticed. Again, over-interpretation should be avoided and no changes are made in response to the Reviewer’s comments. It is hoped that by raising clinicians’ awareness with simplified means to diagnosis, the condition can be readily recognized.
The inappropriate expressions have been removed from the title and the manuscript.
Modern English is accommodative of calques. But I agree with the Reviewer that this should be avoided in scientific publications. The manuscript has been amended accordingly.
Confidence intervals have been added to the Fisher’s exact test when statistically significant P values are found. As this is not a systematic review with meta-analysis, I do not go into the full extent with correction for multiple comparison, justification for exploratory analyses, or missing data strategy. More importantly, the limitations on the exploratory nature of the manuscript are highlighted in the Limitations (Lines 352-360). The bias when pooling data from multiple case reports is also cautioned.
As said, Tables 2 to 4 have been moved to the Supplementary file. Thank you for the suggestion.
I agree with the Reviewer that prospective validation is needed for assessing the role of identifying grey platelets in the initial diagnosis. Indeed, even light transmission platelet aggregometry as a confirmation test has not been prospectively evaluated. Collaboration and prospective evaluation are the way forward (Lines 351, 369-371). On the other hand, the similarities beyond platelet morphology between APDE and grey platelet syndrome are interesting. First, the pattern of abnormalities on light transmission platelet aggregometry is almost identical for the two disorders (Lines 275-276). Second, the clinical manifestations of grey platelet syndrome include not only thrombocytopathy, but also a range of immune dysregulation and autoimmunity (Lines 291-293). These points have been added to the manuscript.
The frequent use of individual case reports is indeed a limitation of the review because of a high tendency for biased observations. This is highlighted in the Limitations. (Lines 353-360)
The Reviewer’s suggestion for a separation section about limitations of the study has been added. (Lines 353-360)

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The Authors made the paper more understandable and fluent. They followed quite completely the requests and they changed the text appropriately. No criticisms were added by me.

Author Response

Thank you very much for taking time to scrutinize the revised manuscript again.

Reviewer 3 Report

Comments and Suggestions for Authors

Dear Authors,

Thank you for your detailed and thoughtful response to the reviewer’s comments, as well as for the substantial revisions made to the manuscript. The effort to address the concerns is clearly visible, and the manuscript has improved in several important aspects.

While the methodological transparency has improved, the review still lacks elements that would strengthen reproducibility (e.g., more detailed search strategy, structured framework). I understand the constraints of a narrative review; however, further clarification of the methodological approach would still be beneficial.
The discussion of diagnostic approaches (e.g., grey platelets as a screening tool) is more balanced, but remains largely hypothesis-generating and would benefit from clearer positioning as such within the manuscript.
The manuscript does not include any form of quality assessment of the included studies, nor does it clearly differentiate the weight of evidence from observational studies versus case reports. This should be addressed at least narratively.

Author Response

Additional clarification of the methodological approach has been made (Lines 81-83).
I agree that the finding of grey platelets as a screening tool needs to be better positioned as a hypothesis-generating proposition. Additional remarks are made (Lines 276-278).
The lack of quality assessment for the included studies is indeed another limitation. This is now properly addressed (Lines 366-368).

I hope these changes will satisfy the queries. Thank you again for taking time to go over the manuscript again.