Macrophages drive inguinal fat pad and lymph node remodelling in response to peripheral inflammation

Reviewer #1 (Public review):

The idea is super interesting, and the subsequent work is potentially significant because it links peripheral inflammation to remodelling of perinodal adipose tissue and draining lymph nodes. This suggests an antigen-independent manner by which local tissue inflammation can communicate with and reshape immune organ structure and tissue metabolism. However, the evidence is suggestive. For instance, many conclusions rely on correlational weight/cellularity relationships, models with confounders (spontaneous wounding; potentially systemic IMQ), and macrophage dependence inferred from a single pharmacologic approach without definitive depletion/lineage or tracer-based causal link.

Comments on revised version:

Overall, the rebuttal addresses most of the original concerns constructively, with additional data and appropriate moderation of several claims. However, some of the key mechanistic conclusions remain over-stated. In particular, macrophage origin, the contribution of systemic inflammation, and the mechanistic relationship between fat-pad remodelling and lymph-node expansion remain incompletely resolved. The manuscript would nevertheless be acceptable if these limitations are clearly acknowledged and the mechanistic language toned down. That said, I think the rebuttal is broadly satisfactory.

Reviewer #2 (Public review):

Summary:

The authors aim to demonstrate skin inflammation is associated with fat pad atrophy and lymph node expansion. They further propose that these phenotypes are driven by the recruitment and lipid metabolism of CCR2-independent macrophages.

The authors took advantage of two skin inflammation models, fight-induced and imauimod-induced skin inflammation and analyzed multiple tissues, including skin, fat pads, and lymph nodes. Using a macropahge-depletion method (e.g., CSF-1R inhibitor), the authors further suggest the inverse correlation between fat pads atrophy and lymph node expansion is macropahge-dependent.

Comments on revised version:

The authors improved their manuscript with additional data and discussion. However, the authors need to clarify their terminology in the experiments. To strengthen their conclusion, authors need some additional experiments addressed below.

Clarify cohousing conditions in Fig. 1 through 3: the authors used 'resting' ,'alone', 'together'. These are unclear. Please state whether 'resting' mice were singly housed or co-housed in Fig. 1. If they singly house, specify when they were separated from their littermate or cage mates. In Fig. 1-3. If they were co-housed ('together'), specify whether their cage mates were littermate or non-littermate Ccr2-/- mice in the manuscript, including line 107.

Strengthen the link between fighting and the observed phenotypes: Co-housed Ccr2-/- males had increased lymph node (LN) weight and reduced fat pad weight. To test whether these changes are associated with fighting-induced skin inflammation, please consider comparing mice that are singly housed after three weeks of co-housing with mice that are singly housed throughout the same period.

Clarify the monocyte analysis: At line 141, please use 'monocytes' rather than 'inflammatory monocytes' if the analysis does not include inflammatory markers/phenotypes. Please also label the monocytes and macrophage populations in Fig. 3Di and 3Dii as was done for neutrophils and eosinophils in Fig. 3B.

Recruitment vs. Self-renewal: At line 144, CD11b expression alone does not distinguish recruited cells from cells expanded by local proliferation; Inflammation itself can alter CD11b expression. Please consider providing the evidence that distinguish these possibilities. Fate mapping would be an ideal approach, while Ki67 staining or BrdU incorporation assay could alternatively assess proliferation.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public review):

Major Comments:

(1) "Wounding/fighting" evidence is confounding.

Unless I am mistaken, a large part of the argument for inflammation-driven perinodal fat pad atrophy and LN expansion relies on spontaneous fighting injuries in co-housed CCR2-/- males, including animals "culled...due to excessive wounding." Because wound severity, duration, infection load, stress, and cage dynamics are uncontrolled, isn't it difficult to assign causality to "cutaneous inflammation"?

We thank the reviewer for this point and fully understand the concerns here. We have carefully gone through the text now and ensured that we refer to wounding-associated inflammation throughout. This therefore takes into account potential wound infections etc. We are also confident that the phenotype relates to cutaneous inflammation because it is only seen in lymph nodes and fat pads draining inflamed skin. We have adapted the discussion accordingly to address this important issue (lines 169-172 of the revised text).

(2) The "CCR2-independent macrophage" conclusion.

The manuscript interprets persistence/accumulation of macrophages despite reduced inflammatory monocytes as CCR2-independent recruitment or local proliferation. However, CCR2 deficiency can alter immune baselines and long-term tissue remodelling. Perhaps consider bone marrow chimeras (WT to CCR2-/-, CCR2-/- to WT ????) or an inducible CCR2 deletion approach to separate developmental/systemic effects from acute inflammation-driven mechanisms. If "in situ proliferation" is proposed, include a direct readout (e.g., Ki67 in ATMs in the fat pad).

We have previously published that CCR2-/- mice display no alterations in any myeloid or lymphoid cell subsets with the exception of Ly6C+ monocytes. We have now referred to this in the revised text (lines 135 and 136) and hope that this addresses the reviewer’s concerns. In terms of whether the CCR2-independent increase in macrophages as a consequence of recruitment or local proliferation, the fact that the macrophages are CD11b+, along with the relative increase in inflammatory monocyte content in co-housed CCR2-/- mouse skin, strongly suggests that they derive from peripheral blood monocytes and therefore from recruited cells. We have clarified these points on page 7 of the revised text.

(3) IMQ and systemic effects.

The work relies on topical Aldara/imiquimod as an "inflammation without antigen" driver of distal LN/fat-pad remodelling. But IMQ is well known (and cited by the authors) to enter circulation and drive systemic responses, which could blur whether effects are truly draining-site specific vs systemic metabolic/inflammatory effects. It would be ideal to provide systemic context: plasma cytokines and/or metabolic readouts (e.g., circulating FFAs) to distinguish local vs systemic drivers.

This is an important point. We have now included plasma cytokine data showing that these are indeed elevated systemically in Aldara-treated mice (new Supplementary Figure 5). We have altered our discussion of this point to reflect these new data (lines 228-229 of the revised text).

(4) Macrophage dependence is inferred from CSF1R inhibitor treatment.

However, validation of macrophage depletion and specificity is incomplete. The manuscript uses AZD7507 (CSF1R inhibitor) and observes partial rescue of fat pad/LN phenotype while skin severity (PASI) is unaffected. But, to this reviewer, the data shown do not clearly quantify actual macrophage depletion efficiency in the target fat pad, and LN at endpoint, and CSF1R blockade can affect multiple myeloid populations. Therefore, show absolute macrophage counts (and likely other myeloid populations) in fat pad and LN with/without AZD7507 at the analysed timepoints, not only outcome weights. (The methods describe dosing but not endpoint depletion quantification??)

We have now added these data (new Figure 7D and Supplementary Figure S6 and discussed on page 13 of the revised manuscript). What we show is that fat pads from Aldara-treated mice show a large reduction in macrophages and also a reduction in dendritic cells, although the number of dendritic cells was already low in the fat pad of Aldara-treated females. The lymph nodes of Aldara-treated females with AZD7507 also show reduced macrophage counts, but the reduction is also seen in all other immune subsets (lymph nodes were smaller so reduced counts in all subsets). We hope that these new data satisfy the reviewer’s concerns.

(5) Fat pad atrophy/LN expansion is a correlation.

The paper emphasises negative correlations between fat pad and LN weights/cellularity at baseline and with inflammation. But correlation does not establish whether fat pad lipolysis drives LN expansion, whether LN changes drive fat remodelling, or whether both reflect systemic mediators. Add tissue-level evidence distinguishing true adipocyte loss vs other contributors to "weight change" (e.g., oedema/fibrosis).

We agree that our data do not establish a direct causal relationship between adipose tissue loss and LN expansion, but the observations do demonstrate a strong temporal association. As seen from the added graph (new Figure 8B and related text on page 13 of the revised manuscript), the rapid and concurrent occurrence of both processes (approximately 25% reduction in fat pad weight and 30% increase in LN size within 24 h of Aldara treatment) suggests that they are closely linked biological events occurring within the same tissue microenvironment. Determining whether these changes arise through direct local interactions or reflect broader inflammatory mediators would require additional mechanistic investigation.

(6) Evidence for "fatty acid donation" from fat pad to LN.

The lipid data are described as "exemplary," and the inference that LN fatty acids originate from the fat pad is based on temporal ordering and relative abundance. This does not rule out plasma spillover, LN-intrinsic metabolism, or altered lymph flow.

We agree with reviewer and have amended our discussion of this point appropriately (page 16 of the revised manuscript).

Reviewer #2 (Public review):

The authors aim to demonstrate skin inflammation is associated with fat pad atrophy and lymph node expansion. They further propose that these phenotypes are driven by the recruitment and lipid metabolism of CCR2-independent macrophages.

The authors took advantage of two skin inflammation models, fight-induced and imauimod-induced skin inflammation and analyzed multiple tissues, including skin, fat pads, and lymph nodes. Using a macropahge-depletion method (e.g., CSF-1R inhibitor), the authors further suggest the inverse correlation between fat pads atrophy and lymph node expansion is macropahge-dependent. While the study identifies this intriguing inverse correlation during skin inflammation, the causal pathway linking fat pad atrophy and lymph nodes enlargement has not been clearly established.

To improve the rigor of the manuscript, the authors address the following concerns;

(1) CCR2-deficient mice showed reduced inflammatory monocytes and monocyte-derived macrophages (PMID:16462739; 16341265). During tissue inflammation, CCR2+ classical monocytes are typically recruited to the injured peripheral tissues, including skin, where they differentiate into monocyte-derived macrophages (PMID:38474365). While inflammatory monocytes were reduced in the skin (Figure 3 d), fat pads (Figure 4a, S2D) of CCR2-deficient mice, macrophage numbers were significantly increased in these mice. It remains unclear whether CCR2-independent macrophages were newly recruited from alternative sources or tissue-resident macrophages underwent local self-proliferation to compensate for the loss of CCR2+ monocyte-derived macrophages.

We agree with reviewer and have expanded our discussion of this important point (see text on pages 7 and 8 of the revised manuscript). As mentioned in response to reviewer 1 we have inferred from the expression of CD11b and c on recruited macrophages that they are derived from peripheral blood monocytes and therefore ultimately are recruited and have not arisen due to local proliferation. We hope that the reviewer is happy with this expanded discussion.

(2) In line 258, the authors state that there was "a significant reduction in CD11C- CD206+ anti-inflammatory macrophages (Figure 4b i-iii)". However, the quantification data in Figure 4b iii do not appear to show any reduction in anti-inflammatory macrophages in either males or females. Please reconcile this discrepancy between the text and the figure

We apologise for our carelessness here and this is the consequence of not having normalised some of the data presented. We have now done this and updated the graph which now, hopefully, more convincingly demonstrate reduction in CD11c- macrophages.

(3) Although CD11C and CD206 were historically used as markers of inflammatory and anti-inflammatory markers, respectively. These markers are no longer considered sufficient to define the macrophage polarization state, particularly in adipose tissue, where they are constitutively expressed by resident macrophages (PMID:34210853). Numerous studies have demonstrated substantial macrophage diversity/heterogeneity across iWAT, eWAT, and brown fat tissues. The authors should discuss adipose macrophage diversity beyond the outdated M1/M2 frame.

We thank the reviewer for pointing this out and apologise for the superficial way in which we have addressed macrophage heterogeneity in the fat pads. We selected CD11c, as it is clearly an important discriminatory marker for tissue macrophages, and CD206 as it presents itself as a common marker of both CD11c-positive and CD11c-negative macrophages in our analyses. We fully acknowledge that the understanding of macrophages has moved on beyond the simple pro-and anti-inflammatory categories have therefore amended the discussion appropriately (please see text on page 8 of the revised manuscript). We hope that these changes are satisfactory for the reviewer.

Minor issues

(1) Clarify which claims are "antigen-independent" vs "no intentional antigen." The introduction/abstract emphasises "absence of antigen presentation," but inflammation models (wounds/IMQ) do not exclude endogenous/self-antigens. Rephrase or add controls aligned to the claim.

We fully accept reviewer’s point here and have removed references to ‘antigen-independent’ throughout.

(2) Provide more explicit randomisation/blinding details for subjective readouts (e.g., PASI scoring).

We agree that additional methodological detail would improve transparency. Inflammation scoring was performed by an independent collaborator blinded to treatment allocation. Animals were not formally randomized between groups because AZD-treated mice required additional gavage procedures and handling distinct from control animals. We have now included additional details in the Materials and Methods section (see page 22 of the revised text).

(3) Increase transparency on sample sizes and independence when pooling tissues (e.g., pooled fat pads, pooled macrophage RNA samples).

Lymph nodes and fat pads were used for different analyses throughout the study, resulting in differences in sample processing and pooling strategies between experiments. Information regarding biological replication and any sample pooling is provided within the corresponding figure legends for each experiment.

In most cases, both fat pads and lymph nodes of each mouse were pooled for analysis, this is specified in each figure legend (i.e. ‘each point represents the combined weight of both inguinal lymph nodes/fat pads for each mouse’

Pooling of fat pads from multiple individual mice was only done for RNA sequencing due to low numbers of adipose tissue macrophages. Again, details are in the figure legends.

We hope that this is acceptable to the reviewer.

(4) Quantify systemic effects of IMQ (weight loss is mentioned in monitoring; include the data and interpret its relevance).

Body weight was monitored throughout the study for animal welfare purposes but was not systematically recorded for analysis. While we cannot formally exclude systemic effects, we believe the observed phenotype is unlikely to be driven primarily by general sickness behaviour, as substantial tissue changes were already evident by day 1 following treatment, including an approximately 25% reduction in fat pad weight and a 30% increase in lymph node weight (please see revised figure 8B). The rapid onset and tissue-specific nature of these changes suggest an early biological response rather than a secondary consequence of generalized illness.

(5) Tone down mechanistic language ("donation," "feeds the LN") unless tracer/intervention experiments are added; keep as "consistent with" until proven.

We thank the reviewer for pointing this out and have amended the language appropriately.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

Minor concerns;

(1) Please delete 'i-iii' from Figure 3b, as these panel labels are not referenced anywhere in the manuscript.

We have carefully edited, and improved, figures throughout the text and hope that they are now acceptable.

(2) Please change '1D' to '2D' in Figure S2.

This has now been done and we apologise for this carelessness.