Differential Regulation of Hepatic Macrophage Fate by Chi3l1 in MASLD

Reviewer #1 (Public review):

The manuscript by Shan et al seeks to define the role of the CHI3L1 protein in macrophages during the progression of MASH. The authors argue that the Chil1 gene is expressed highly in hepatic macrophages. Subsequently, they use Chil1 flx mice crossed to Clec4F-Cre or LysM-Cre to assess the role of this factor in the progression of MASH using a high-fat, high-fructose diet (HFFC). They found that loss of Chil1 in KCs (Clec4F Cre) leads to enhanced KC death and worsened hepatic steatosis. Using scRNA seq, they also provide evidence that loss of this factor promotes gene programs related to cell death. From a mechanistic perspective, they provide evidence that CHI3L serves as a glucose sink and thus loss of this molecule enhances macrophage glucose uptake and susceptibility to cell death. Using a bone marrow macrophage system and KCs they demonstrate that cell death induced by palmitic acid is attenuated by the addition of rCHI3L1. While the article is well written and potentially highlights a new mechanism of macrophage dysfunction in MASH, there are some concerns about the current data that limit my enthusiasm for the study in its current form. Please see my specific comments below.

Major:

(1) The authors' interpretation of the results from the KC ( Clec4F) and MdM KO (LysM-Cre) experiments is flawed. For example, in Figure 2 the authors present data that knockout of Chil1 in KCs using Clec4f Cre produces worse liver steatosis and insulin resistance. However, in supplemental Figure 4, they perform the same experiment in LysM-Cre mice and find a somewhat different phenotype. The authors appear to be under the impression that LysM-Cre does not cause recombination in KCs and therefore interpret this data to mean that Chil1 is relevant in KCs and not MdMs. However, LysM-Cre DOES lead to efficient recombination in KCs and therefore Chil1 expression will be decreased in both KCs and MdM (along with PMNs) in this line.

Therefore, a phenotype observed with KC-KO should also be present in this model unless the authors argue that loss of Chil1 from the MdMs has the opposite phenotype of KCs and therefore attenuates the phenotype. The Cx3Cr1 CreER tamoxifen inducible system is currently the only macrophage Cre strategy that will avoid KC recombination. The authors need to rethink their results with the understanding that Chil1 is deleted from KCs in the LysM-Cre experiment. In addition, it appears that only one experiment was performed, with only 5 mice in each group for both the Clec4f and LysM-Cre data. This is generally not enough to make a firm conclusion for MASH diet experiments.

(2) The mouse weight gain is missing from Figure 2 and Supplementary Figure 4. This data is critical to interpret the changes in liver pathology, especially since they have worse insulin resistance.

(3) Figure 4 suggests that KC death is increased with KO of Chil1. However, this data cannot be concluded from the plots shown. In Supplementary Figure 6 the authors provide a more appropriate gating scheme to quantify resident KCs that includes TIM4. The TIM4 data needs to be shown and quantified in Figure 4. As shown in Supplementary Figure 6, the F4/80 hi population is predominantly KCs at baseline; however, this is not true with MASH diets. Most of the recruited MoMFs also reside in the F4/80 hi gate where they can be identified by their lower expression of TIM4. The MoMF gate shown in this figure is incorrect. The CD11b hi population is predominantly PMNs, monocytes, and cDC,2 not MoMFs (PMID:33997821). In addition, the authors should stain the tissue for TIM4, which would also be expected to reveal a decrease in the number of resident KCs.

(4) While the Clec4F Cre is specific to KCs, there is also less data about the impact of the Cre system on KC biology. Therefore, when looking at cell death, the authors need to include some mice that express Clec4F cre without the floxed allele to rule out any effects of the Cre itself. In addition, if the cell death phenotype is real, it should also be present in LysM Cre system for the reasons described above. Therefore, the authors should quantify the KC number and dying KCs in this mouse line as well.

(5) I am somewhat concerned about the conclusion that Chil1 is highly expressed in liver macrophages. Looking at our own data and those from the Liver Atlas it appears that this gene is primarily expressed in neutrophils. At a minimum, the authors should address the expression of Chil1 in macrophage populations from other publicly available datasets in mouse MASH to validate their findings (several options include - PMID: 33440159, 32888418, 32362324). If expression of Chil1 is not present in these other data sets, perhaps an environmental/microbiome difference may account for the distinct expression pattern observed. Either way, it is important to address this issue.

Reviewer #2 (Public review):

The manuscript from Shan et al., sets out to investigate the role of Chi3l1 in different hepatic macrophage subsets (KCs and moMFs) in MASLD following their identification that KCs highly express this gene. To this end, they utilise Chi3l1KO, Clec4f-CrexChi3l1fl, and Lyz2-CrexChi3l1fl mice and WT controls fed a HFHC for different periods of time.

Firstly, the authors perform scRNA-seq, which led to the identification of Chi3l1 (encoded by Chil1) in macrophages. However, this is on a limited number of cells (especially in the HFHC context), and hence it would also be important to validate this finding in other publicly available MASLD/Fibrosis scRNA-seq datasets. Similarly, it would be important to examine if cells other than monocytes/macrophages also express this gene, given the use of the full KO in the manuscript. Along these lines, utilisation of publicly available human MASLD scRNA-seq datasets would also be important to understand where the increased expression observed in patients comes from and the overall relevance of macrophages in this finding.

Next, the authors use two different Cre lines (Clec4f-Cre and Lyz2-Cre) to target KCs and moMFs respectively. However, no evidence is provided to demonstrate that Chil1 is only deleted from the respective cells in the two CRE lines. Thus, KCs and moMFs should be sorted from both lines, and a qPCR performed to check the deletion of Chil1. This is especially important for the Lyz2-Cre, which has been routinely used in the literature to target KCs (as well as moMFs) and has (at least partial) penetrance in KCs (depending on the gene to be floxed). Also, while the Clec4f-Cre mice show an exacerbated MASLD phenotype, there is currently no baseline phenotype of these animals (or the Lyz2Cre) in steady state in relation to the same readouts provided in MASLD and the macrophage compartment. This is critical to understand if the phenotype is MASLD-specific or if loss of Chi3l1 already affects the macrophages under homeostatic conditions.

Next, the authors suggest that loss of Chi3l1 promotes KC death. However, to examine this, they use Chi3l1 full KO mice instead of the Clec4f-Cre line. The reason for this is not clear, because in this regard, it is now not clear whether the effects are regulated by loss of Chi3l1 from KCs or from other hepatic cells (see point above). The authors mention that Chi3l1 is a secreted protein, so does this mean other cells are also secreting it, and are these needed for KC death? In that case, this would not explain the phenotype in the CLEC4F-Cre mice. Here, the authors do perform a basic immunophenotyping of the macrophage populations; however, the markers used are outdated, making it difficult to interpret the findings. Instead of F4/80 and CD11b, which do not allow a perfect discrimination of KCs and moMFs, especially in HFHC diet-fed mice, more robust and specific markers of KCs should be used, including CLEC4F, VSIG4, and TIM4.

Additionally, while the authors report a reduction of KCs in terms of absolute numbers, there are no differences in proportions. This, coupled with a decrease also in moMF numbers at 16 weeks (when one would expect an increase if KCs are decreased, based on previous literature) suggests that the differences in KC numbers may be due to differences in total cell counts obtained from the obese livers compared with controls. To rule this out, total cell counts and total live CD45+ cell counts should be provided. Here, the authors also provide tunnel staining in situ to demonstrate increased KC death, but as it is typically notoriously difficult to visualise dying KCs in MASLD models, here it would be important to provide more images. Similarly, there appear to be many more Tunel+ cells in the KO that are not KCs; thus, it would be important to examine this in the CLEC4F-Cre line to ascertain direct versus indirect effects on cell survival.

Finally, the authors suggest that Chi3l1 exerts its effects through binding glucose and preventing its uptake. They use ex vivo/in vitro models to assess this with rChi3l1; however, here I miss the key in vivo experiment using the CLEC4F-Cre mice to prove that this in KCs is sufficient for the phenotype. This is critical to confirm the take-home message of the manuscript.

Reviewer #3 (Public review):

This paper investigates the role of Chi3l1 in regulating the fate of liver macrophages in the context of metabolic dysfunction leading to the development of MASLD. I do see value in this work, but some issues exist that should be addressed as well as possible.

Here are my comments:

(1) Chi3l1 has been linked to macrophage functions in MASLD/MASH, acute liver injury, and fibrosis models before (e.g., PMID: 37166517), which limits the novelty of the current work. It has even been linked to macrophage cell death/survival (PMID: 31250532) in the context of fibrosis, which is a main observation from the current study.

(2) The LysCre-experiments differ from experiments conducted by Ariel Feldstein's team (PMID: 37166517). What is the explanation for this difference? - The LysCre system is neither specific to macrophages (it also depletes in neutrophils, etc), nor is this system necessarily efficient in all myeloid cells (e.g., Kupffer cells vs other macrophages). The authors need to show the efficacy and specificity of the conditional KO regarding Chi3l1 in the different myeloid populations in the liver and the circulation.

(3) The conclusions are exclusively based on one MASLD model. I recommend confirming the key findings in a second, ideally a more fibrotic, MASH model.

(4) Very few human data are being provided (e.g., no work with own human liver samples, work with primary human cells). Thus, the translational relevance of the observations remains unclear.