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Avalilação PREreview de Antigen-specific CD8 T cells are generated and reactivated in the bone marrow following viral brain infections and impact the bone marrow niche

Publicado
DOI
10.5281/zenodo.24276426
Licença
CC BY 4.0

In their manuscript, “Antigen-specific CD8 T cells are generated and reactivated in the bone marrow following viral brain infections and impact the bone marrow niche”, Anani-Wolf et al investigate the extent to which antigen-specific CD8 T cell priming, expansion and memory formation can happen in the bone marrow (BM) after an infectious or inflammatory brain insult using a mouse model of TMEV intracranial infection or OVA+polyI:C.

Antigen-specific CD8 T cells (VP+) increased in number and ratios in the bone marrow in a manner that was insensitive to secondary lymph node egress blockade (FTY720 treatment). Most of these cells were found by IV staining to be in the parenchyma. The same experiments after restimulation with a defined peptide show a surge in VP+ CD8 T cells in the BM (FTY720 insensitive and IV-).

The authors attempt to further explain how this brain-marrow interaction is mediated and propose APCs with migratory potential (CD11b+MHCII+CD103+) as the major transporters of antigen from the brain to the marrow given as these cells co-stain with OVA-AF488+ cells and were found in both organs.

Finally, they interrogate the effect of BM-lodged CD8 T cell reactivation on the homeostasis of HSPCs by quantifying LSK cells, and document increase in LSK cell ratios in the BM. This was associated with a CD8 T cell-dependent influx of CD11b+MHCII+ APCs.

This work contributes to the body of evidence characterizing the bone marrow as a unique site where the primary lymphoid niche and secondary lymphoid niche could coexist, and how the activity of the latter in response to peripheral insults could shape the progenitor niche.

The model put forward by the authors of BM in situ CD8 T cell priming, expansion, and tissue-resident memory formation can be hypothesized from the body of data taken together with other works in the literature. However, the methodology employed does not unequivocally prove that VP+ T cells are of BM origin or that the memory cells are true tissue-resident memory cells. The same can be said about the migratory potential of the APCs. These claims would ideally require an origin-tracing experiment or a more comprehensive characterization of the cellular program to rigorously demonstrate cell identity. In the absence of such experimental evidence, it would be more cautious to soften the conclusions and acknowledge the limitations of the study in the discussion.

Major Comments:

1. The models with FTY720 treatment show that the increase in antigen-specific CD8 T cells in the bone marrow following primary infection/stimulation and memory reactivation are independent of lymph node egress. The IV labeling demonstrates that these cells are in the parenchymal space and not recent immigrants. However, influx of antigen-specific CD8 T cells primed in the spleen cannot be excluded as spleen egress is less S1P1-dependent and IV CD45 labeling shows that at least 20-40% of the antigen-specific CD8 T cells are IV+. Performing the same experiments in splenectomized mice would eliminate the possibility of priming in the spleen and argue more strongly for BM in situ priming and expansion.

2. Tissue residency implies a specific residency program. Insensitivity to FTY720 indicates that the responding cells do not derive from recirculating populations exiting secondary lymphoid organs, and IV labeling would indicate they are not in the vascular compartment at harvest, but neither observation definitively identifies them as bona fide tissue-resident memory cells. This is particularly relevant in bone marrow, which is highly vascularized (as shown by the high efficiency of CD8 T cell depletion using low dose antibodies) and known to host recirculating memory T cells. To support a claim of tissue residency, the authors could either provide further characterization — immunophenotyping with a combination of markers (e.g., CD69, CD49a, CD62L, CCR7, S1PR1), a transcriptional program consistent with residency, or functional evidence from parabiosis, transfer, or tracing experiments — or revise the terminology to describe these cells as a locally responding, egress-independent population. As CD69 is an activation marker, combining it with other markers or comparing it with the irrelevant-peptide control group would strengthen phenotyping after peptide recall.

3. The migratory potential of the AF488+ CD11b+MHCII+ cells is based on expression of a single marker CD103.

a. CD103, as the authors rightly state, “is associated with migratory potential”. The identification of CD103 as a marker for APCs with migratory potential is mostly in the context of dendritic cells in mucosal sites. The validity of this marker to identify such populations in the context of brain inflammation seems to be less established in the current literature. CD103 is also not directly responsible for the migratory mechanism, as is the case for CCR7.

b. Although, the authors show that phenotypically similar cells are AF488+ in the brain and in the BM, there is no evidence that these cells have migrated from one compartment to another. Importantly, the authors cannot rule out antigen leakage from the brain into systemic circulation or viremia followed by uptake of mirroring APCs in the BM.

Can the authors provide evidence for expression of proteins of the migratory machinery (CCR7) or functional proof of migratory capacity (chemotaxis assays)? Alternatively, experiments prospectively tracing these APCs would provide more definitive proof for the model put forth.

Minor Comments:

  1. The manuscript would benefit from using more precise phrasing and terminology to better articulate the observations of the authors and their inferred model/hypothesis.

    1. On multiple occasions, the term “generated” is used to interpret the increase in number and/or ratio of antigen-specific CD8 T cells. This terminology is ambiguous as this could mean the development of these cells, their expansion, or their maturation. Using a more precise term would help avoid ambiguities for the reader.

    2. page 46: “However, antigen-specific reactivation of Db: VP2+ CD8 T cells resulted in a massive dysregulation of LSK cells in the femoral bone marrow, exhibited by expansion in the absence of active viral infection or danger signals”.

i. “Dysregulation” is a vague term. A more descriptive term (such as “LSK expansion”) would help clarify what precise experimental observation the authors are referring to.

ii. “Danger signals”. I would encourage the authors to replace this term with a description of what was actually controlled in the experiment. As written, the phrase is ambiguous (it is applied in the literature to exogenous PAMPs, endogenous DAMPs, and inflammatory cytokines alike. More importantly, the stated absence is not something the authors can establish. Reactivated effector CD8 T cells themselves produce IFN-γ and TNF, both of which act on HSPCs and promote emergency myelopoiesis, and antigen-driven cytotoxicity would be expected to release endogenous alarmins or so-called danger-associated molecular patterns. The claim therefore sits uneasily with the mechanism the authors are proposing.

iii. “massive” is a qualitative term that can be hyperbolic. A more neutral description (such as “significant” or “marked”) could be used.

  1. Page 23: “To avoid caveats of neuronal damage from an actual viral infection, we intracranially administered AF488-labeled-OVA peptide antigen with Poly I:C (OVA-PIC ic) into the brain.” Since TLR stimulation with poly I:C induces inflammation and can lead to cell death, poly I:C associated neuronal damage (or damage of other resident glial cells or circulating cells) cannot be eliminated. The authors themselves describe their model as an inflammatory model later in the text. Specifying what virus-related damages they intended to control for would help resolve what could appear to be inconsistencies.

  • Page 23, “Flow cytometry analysis showed AF488 expression in a significant number of CD45+ cells indicating that OVA has been phagocytosed and retained within the brain 5-7 days post injection”. At this point in the manuscript, the data shows co-staining of CD45 and AF488. It would be more appropriate to place the conclusion that OVA has likely been phagocytosed at the end of the paragraph after the whole body of data supporting this has been presented.

  • Showing representative flow charts illustrating the gating strategies of multidimensional panels would give further transparency and confidence in the validity of the quantification data presented.

  • Page 33: “Two days before euthanasia, mice received either the E7 peptide (control peptide that does not reactivate TMEV specific CD8 T cells) …”. Authors present E7 peptide as a control peptide that does not reactivate TMEV-specific CD8 T cells. It would be helpful for the critical reading of the manuscript if more information concerning this peptide were provided, particularly from which pathogen it was derived and whether cross-reactivity with VP can be eliminated.

  • Page 34: “These data indicate that CD8 T cells directly lead to an influx of MHCII+ myeloid cells within the bone marrow following antigen-specific reactivation…” While the data supports the premise that CD8 T cells are necessary, demonstrating a mechanism as to how they do this would better support the direct effect. In this regard, the wording of later conclusions (e.g. “LSK dysregulation and myeloid cell influx into the femoral bone marrow was CD8-dependent”) is more appropriate.

I reviewed this preprint as part of the Transparent and Accountable Peer Review training program. This report was written with the support of my research mentor.

Competing interests

The authors declare that they have no competing interests.

Use of Artificial Intelligence (AI)

The authors declare that they did not use generative AI to come up with new ideas for their review.

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