Tolerance to Lung Infection in TWIK2 K⁺ Efflux Mediated Macrophage Trained Immunity

Reviewer #1 (Public review):

Summary:

Alveolar macrophages (AMs) are key sentinel cells in the lungs, representing the first line of defense against infections. There is growing interest within the scientific community in the metabolic and epigenetic reprogramming of innate immune cells following an initial stress, which alters their response upon exposure to a heterologous challenge. In this study, the authors show that exposure to extracellular ATP can shape AM functions by activating the P2X7 receptor. This activation triggers the relocation of the potassium channel TWIK2 to the cell surface, placing macrophages in a heightened state of responsiveness. This leads to the activation of the NLRP3 inflammasome and, upon bacterial internalization, to the translocation of TWIK2 to the phagosomal membrane, enhancing bacterial killing through pH modulation. Through these findings, the authors propose a mechanism by which ATP acts as a danger signal to boost the antimicrobial capacity of AMs.

Strengths:

This is a fundamental study in a field of great interest to the scientific community. A growing body of evidence has highlighted the importance of metabolic and epigenetic reprogramming in innate immune cells, which can have long-term effects on their responses to various inflammatory contexts. Exploring the role of ATP in this process represents an important and timely question in basic research. The study combines both in vitro and in vivo investigations and proposes a mechanistic hypothesis to explain the observed phenotype.

Weaknesses:

The authors have revised the manuscript to address the comments raised during the first round of review. However, several figures, figure legends, and methodological sections still require additional adjustments and clarification.

The interpretation of CFU from lysates as 'killing' is unclear; lysate CFUs typically reflect intracellular surviving bacteria and are confounded by differences in uptake. Please include an uptake control (early time point) or time-course to distinguish phagocytosis from intracellular killing. Also, clarify how bacterial burden was calculated (supernatant vs cell-associated vs total). Supernatant alone may not capture adherent bacteria. The normalization as 'fold killing' (mean negative control / sample) is non-standard; please report absolute CFU (log scale) and specify the exact definition of killing/survival.

The Methods section is largely incomplete and requires substantial revision. For instance, the authors report quantification of cytokine concentrations, yet no information is provided regarding how these measurements were performed. It is unclear whether cytokines were measured in BALF by ELISA, or assessed at the mRNA level by qPCR from total lung lysates, or by another method. This information must be clearly specified. In addition, the rationale for selecting the measured cytokines should be justified. While the choice of IL-1β and IL-6 is relatively straightforward, the focus on IL-18 requires explicit justification.

Similarly, the methodology used to quantify immune cell populations presented in Figure 2 is not described. It is not stated how immune cells were isolated and identified (e.g. flow cytometry from lung tissue). No information is provided regarding tissue digestion, cell isolation procedures, or gating strategy (presumably by flow cytometry). These details are essential and should be included, together with the corresponding gating strategy and absolute cell numbers.

Moreover, immune cell quantification would be expected in the context of the challenge experiment as well. Reporting unchanged percentages of lung immune cells following ATP exposure does not support the conclusion of a training effect, particularly one that is specific to alveolar macrophages (AMs). In addition, AMs are not considered recruited immune cells; this should be corrected in the figure legend and throughout the manuscript where applicable.

There are inconsistencies throughout the manuscript. For example, the authors report n = 5 for the survival curves in the figure legend, whereas n = 7 is stated in the Methods section. This discrepancy is unclear and should be clarified.

Supplementary Fig. 1 contains major conceptual errors. The volcano plot represents ATAC-seq peaks (differentially accessible chromatin regions), yet the figure, legend, and color scale repeatedly refer to 'genes' and 'differentially expressed genes'. This conflates chromatin accessibility with gene expression and is misleading. Peaks are secondarily annotated to nearby genes, which should be clearly described as an annotation step rather than the unit of analysis. The figure should be revised to explicitly present peak-level statistics (DARs), with gene names shown only as optional annotations. Additionally, the use of simultaneous P < 0.05 and Q < 0.05 thresholds is non-standard, and the absence of down-regulated regions in the plot requires explanation.

In Figure 7, trained WT and Nlrp3⁻/⁻ mice display similar levels of bacterial clearance. How should this result be interpreted?

Overall, while the study addresses an interesting biological question, the manuscript would benefit from substantial revision prior to publication. In particular, clarifications and improvements regarding the methodology, data presentation, and interpretation are required to strengthen the rigor and reproducibility of the conclusions.

Reviewer #2 (Public review):

Summary:

In this manuscript, Thompson et al. investigate the impact of prior ATP exposure on later macrophage functions as a mechanism of immune training. They describe that ATP training enhances bactericidal functions which they connect to the P2x7 ATP receptor, Nlrp3 inflammasome activation, and TWIK2 K+ movement at the cell surface and subsequently at phagosomes during bacterial engulfment. This is an incremental addition to existing literature, which has previously explored how ATP alters TWIK2 and K+, and linked it to Nlrp3 activation. The novelty here is in discovering the persistence of TWIK2 change and exploring the impact this biology may have on bacterial clearance. Additional experiments could strengthen their hypothesis that the in vivo protective effect of ATP-training on bacterial clearance is mediated by alveolar macrophages.

Strengths:

The authors demonstrate three novel findings: 1) prolonged persistence of TWIK2 at the macrophage plasma membrane following ATP that can translocate to the phagosome during particle engulfment, 2) a persistent impact of ATP exposure on remodeling chromatin around nlrp3, and 3) administering mice intra-nasal ATP to 'train' lungs protects mice from otherwise fatal bacterial infection.

Weaknesses:

(1) Some methods remain unclear including the timing and method by which lung cellularity was assessed in Figure 2. It is also difficult to understand how many mice were used in experiments 1, 2 and 6 and thus how rigorous the design was. A specific number is only provided for 1D and the number of mice stated in legend and methods do not match.

(2) The study design is not entirely ideal for the authors' in vivo question. Overall, the discussion would benefit from a clear summary of study caveats, which are primarily that that 1) in vitro studies attributing ATP training-mediated bacterial killing to persistent TWIK2 relocation, K+ influx, a glycolytic metabolic shift , and epigenetic nlrp3 reprogramming were performed in BMDM or RAW cells and not primary AMs, 2) data does not eliminate the possibility that non-AM immune or non-immune cells in the lung are "trained" and responsible for ATP-mediated protection in vivo; flow data examined total lung digest which may obscure important changes in alveolar recruitment, and 3) in vivo work shows data on acute bacterial clearance but does not explore potential risks that "training" for a more responsive inflammasome may have for the severity of lung injury during infection.

(3) The is some lack of transparency on data and rigor of methods. Clear data is not provided regarding the RNA-sequencing results. Specific identities of DEGs is not provided, only one high-level pathway enrichment figure. It would also be ideal if controls were included for subcellular fractionating to confirm pure fractions and for dye microscopy to show negative background.

(4) In results describing 5A, the text states that "ATP-induced macrophage training effects, as measured by augmented bactericidal activity, were diminished in macrophages treated with protease inhibitors". However, these data are not identified significant in the figure; protease dependence can be described as a trend that supports the authors' hypothesis but should not be stated as significant data in text.

In summary, this work contains some useful data showing how ATP can train macrophages via TWIK2/Nlrp3. Revisions have significantly improved methods reporting, added some data to strengthen the conclusions, and toned down on overstatements to bring conclusions more in line with data presented. The title still overstates what the authors have actually tested, since no macrophage-specific targeting in vivo (no conditional gene deletion, macrophage depletion etc) was performed in infection studies. However, in vitro data provide clear evidence that macrophages can be trained by ATP, and through caveats remain, it is plausible that macrophage training is a key mechanism for the protection observed here in the lung.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

(1) First, the concept of training or trained immunity refers to long-term epigenetic reprogramming in innate immune cells, resulting in a modified response upon exposure to a heterologous challenge. The investigations presented demonstrate phenotypic alterations in AMs seven days after ATP exposure; however, they do not assess whether persistent epigenetic remodeling occurs with lasting functional consequences. Therefore, a more cautious and semantically precise interpretation of the findings would be appropriate.

In response, we have performed epigenetic analysis (ATAC seq analysis) as requested (Supp Fig. 1).

(2) Furthermore, the in vivo data should be strengthened by additional analyses to support the authors' conclusions. The authors claim that susceptibility to Pseudomonas aeruginosa infection differs depending on the ATP-induced training effect. Statistical analyses should be provided for the survival curves, as well as additional weight curves or clinical assessments. Moreover, it would be appropriate to complement this clinical characterization with additional measurements, such as immune cell infiltration analysis (by flow cytometry), and quantification of pro-inflammatory cytokines in bronchoalveolar lavage fluid and/or lung homogenates.

We have added the statistical analyses provided for the survival curves (new Fig. 1D), immune cell infiltration analysis, and quantification of pro-inflammatory cytokines in the lung (new Figs. 1, 2).

(3) Moreover, the authors attribute the differences in resistance to P. aeruginosa infection to the ATP-induced training effect on AMs, based on a correlation between in vivo survival curves and differences in bacterial killing capacity measured in vitro. These are correlative findings that do not establish a causal role for AMs in the in vivo phenotype. ATP-mediated effects on other (i.e., non-AM) cell populations are omitted, and the possibility that other cells could be affected should be, at least, discussed. Adoptive transfer experiments using AMs would be a suitable approach to directly address this question.

We have performed additional experiments and found that the numbers of lung macrophages were not significantly altered before and after ATP training (new Fig. 2), indicating the training effects are focused on lung resident macrophages.

Reviewer #2 (Public review):

(1) Missing details from methods/reported data: Substantial sections of key methods have not been disclosed (including anything about animal infection models, RNA-sequencing, and western blotting), and the statistical methods, as written, only address two-way comparisons, which would mean analysis was improperly performed. In addition, there is a general lack of transparency - the methods state that only representative data is included in the manuscript, and individual data points are not shown for assays.

We have revised the methods and statistical analysis.

(2) Poor experimental design including missing controls: Particularly problematic are the Seahorse assay data (requires normalization to cell numbers to interpret this bulk assay - differences in cell growth/loss between conditions would confound data interpretation) and bacterial killing assays (as written, this method would be heavily biased by bacterial initial binding/phagocytosis which would confound assessment of killing). Controls need to be included for subcellular fractionating to confirm pure fractions and for dye microscopy to show a negative background. Conclusions from these assays may be incorrect, and in some cases, the whole experiment may be uninterpretable.

Seahorse assay methodology was updated to confirm the order of cell counting, time at seeding and cell counts. Methods were also updated to address the distinction between bacterial killing (Fig. 1B) and overall decrease in bacterial load.

(3) The conclusions overstate what was tested in the experiments: Conceptually, there are multiple places where the authors draw conclusions or frame arguments in ways that do not match the experiments used. Particularly:

(a) The authors discuss their findings in the context of importance for AM biology during respiratory infection but in vitro work uses cells that are well-established to be poor mimics of resident AMs (BMDM, RAW), particularly in terms of glycolytic metabolism.

We have adjusted the text to reflect that the metabolic assay was performed on BMDMs. AMs are fragile for certain manipulations in vitro. We expect that the metabolic change is similar across several macrophage systems as well as the bacterial load reduction.

(b) In vivo work does not address whether immune cell recruitment is triggered during training.

We have performed immune cell infiltration analysis (new Fig. 2).

(c) Figure 3 is used to draw conclusions about K+ in response to bacterial engulfment, but actually assesses fungal zymosan particles.

We have corrected this in the manuscript.

(d) Figure 5 is framed in bacterial susceptibility post-viral infection, but the model used is bacterial post-bacterial.

We have corrected this in the manuscript.

(e) In their discussion, the authors propose to have shown TWIK2-mediated inflammasome activation. They link these separately to ATP, but their studies do not test if loss of TWIK2 prevents inflammasome activation in response to ATP (Figure 4E does not use TWIK2 KO).

We have now added the TWIK2 KO results (new Fig. 5E).

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

As noted in the public review, it would be advisable to further characterize the in vivo phenotype in order to strengthen the conclusions. Specifically, it would be useful to quantify the bacterial load in the bronchoalveolar lavage fluid and lung homogenates, as well as to measure cytokine levels both in the respiratory compartment and systemically. Additionally, a broader characterization of the immune response in the presence or absence of ATP-induced training would be valuable. In the absence of direct evidence demonstrating that trained AMs mediate the observed phenotype, the authors should adopt a more cautious interpretation of their results. Moreover, careful attention to semantic accuracy is recommended. The concept of trained immunity refers specifically to long-term epigenetic reprogramming that leads to an altered response of target cells upon a secondary challenge, distant from the initial stress. The data presented do not fully demonstrate this phenomenon, and the interpretations should remain aligned with the evidence provided.

Bacterial load has been quantified (see more details in the Methods part). And we also measured immune cell infiltration, quantification of pro-inflammatory cytokines in the lung (new Figs. 1, 2), and epigenetic evaluation of vehicle- and ATP-treated cells (Supp. Fig. 1).

Reviewer #2 (Recommendations for the authors):

(1) It cannot be overstated how lacking the methods are. This includes no discussion of IACUC approval for animal procedures, which must be included as part of research ethics. It also needs to be made clear where raw data is being archived. This notably includes an accession for deposited RNA-sequencing data, although unmanipulated microscopy and western blot images should also be shown. Methods should discuss any pre-processing that occurred with images.

We have revised the methods in the manuscript.

(2) Per statistics, in addition to generally providing more detail and adjusting analyses if they have not been correctly performed, please disclose if SD or SEM is shown. Reporting aggregate data versus representative data would provide more rigor. Perhaps replicate experiments could be included in the supplemental if they cannot, for some reason, be aggregated. Detailed statistical methods for RNA-seq analysis also need to be included.

More details have been provided in the methods section.

(3) It is unclear whether bacterial killing assays were correctly designed and can be interpreted. What does cells collected mean? If the assay was focused on intracellular macrophage bacterial load, it is critical to assess and report phagocytosis since different input loads would confound the assessment of killing. A rigorous wash or an antibiotic to eliminate extracellular bacteria should also have been performed and be described in this case. If the total bacterial burden was assessed, that would use cells+media and also needs to be clear and described. With the information provided, it is unclear whether the assays performed are sufficiently rigorous to assess bacterial killing. In addition, Figure 1B reports using an MOI of 50-100, but all data is compiled in one graph - data from different levels of infection should be separated. Figure 5A shows a model with E.coli followed by PA, but that does not appear to be how the assay was structured in B or C. This also does not match how the experiment is written in the results section, which references S. aureus. It is unclear what tissue (or cells) were assessed in Figure 5. Whole lung? BAL? As written, no data provided regarding bacterial killing is of sufficient quality to be considered valid.

We have re-written the bacterial killing assay in the manuscript. The methodology was corrected to distinguish bacterial killing vs load decrease and generally accurate methodology.

(4) The in vitro data provide reasonable evidence that BMDM/RAW macrophage training can occur in response to ATP exposure. However, it is unclear whether training is an important mechanism for resident AM in vivo, or whether, in vivo, a broader inflammatory response is generated, recruiting additional immune cells that persist and change infection susceptibility. The authors argue for resident AM immune training, but do not provide sufficient evidence to counter the latter possibility (resident AM are never themselves directly assessed, and the presence of other immune cells in vivo is not excluded). See Iliakis et al 2023 (PMID 37640788) for discussion of how this issue continues to drive uncertainty in the field. For this study, at least providing flow cytometry data quantifying myeloid and lymphoid immune populations in BALF before and after various treatments would help address this caveat. Without knowing this, it also confounds the interpretation of Figure 1B; if BAL is not pure AM after training, perhaps 1B could be repeated with ex vivo training or resident AM could be purified?

We have performed immune cell infiltration analysis in the lung (both to BALF and in-tissue, new Fig. 2).

(5) Figure 3A appears to show that fewer than 50% of cells express GFP. Is it expected that only a fraction of RAW cells express TWIK2-GFP? How was this addressed in the analyses for Figure 3? Were cells not appearing to express any significant GFP, included in phagosomal-negative or excluded from analysis? Please include in the methods.

The RAW cells were transfected with TWIK2-GFP and variable GFP expression was expected. These cells were expressing a non-integrated transgene, which has been added to the methods as well as the consideration of cells for the analysis. Cells without visible GFP expression were excluded.

(6) Why are many data points in Figure 3D negative? This suggests that settings were not optimized for microscopy - perhaps there is a very high background signal and the ION stain is barely above it. This is concerning for the quality of data. Further, is it expected that only some cells are positive for ION K+? The images shown clearly differentiate phagosomal K with ATP versus the absence of K without, but it is surprising that some cells appear not to contain any ION K+ signal (not completely clear given lack of brightfield or other cell staining) - this may again point to issues with imaging settings that confound data interpretation. This analysis should be carefully assessed.

This has been updated in the methodology. In old Fig. 3D (new Fig. 4D), the presented data is the net intensity of the phagosome, subtracting the average cytoplasmic MFI from that of the area corresponding to an engulfed zymosan-af594 bead. Thus, a negative value has higher cytoplasmic IonK signal than that of the phagosome.

(7) The Discussion states that it will be interesting to test whether ATP-TWIK2 is a common mechanism of training and specifically references LPS as an ATP-generating signal. However, Figure 2D data show that LPS induces only transient TWIK2 translocation; the authors have data suggesting that, in the context of LPS, TWIK2 'training' will not be engaged. This line of discussion shows incomplete consideration of the data.

We have further limited this language in the text such that this may require differential sensitivity/damage sustained by macrophages as compared to that of epi/endothelial cells in response to bacterial endotoxin.

(8) For RNA-sequencing, plots of the actual genes changed for the mitochondrial pathways of interest would be helpful information for readers, as would a heat map showing sample purity between groups for macrophage markers versus possible contaminant cells, which can also be generated from precursors in BMDM cultures. In general, information in Methods regarding how the analyses in Figure 4B were run is necessary, per cutoffs used to determine DEGs, number of samples in each group, sex of samples used, etc. Greater transparency of data would be appreciated, so plots that show variation between replicates, such as heat maps, would be ideal. Supplemental tables would also be nice.

We have added to the methodology of the RNA sequencing analysis

(9) The use of alternate DAMPs is a positive addition to the experimental design, but no data is given regarding the concentrations used. Ideally, positive controls showing histones/NAD are used at acutely activating concentrations could be included but at least references supporting the doses chosen or information about how doses were selected should be given. It is easy to find substantial literature on histones as a DAMP, but it was unclear why/how NAD was selected.

We have added these concentrations and corresponding references.

(10) The E.coli CFU reported in Figure 5B are extraordinarily low. In addition, CFU are generally shown on a log scale, but this appears to be linear. Please confirm that these data are correct. Perhaps improved methods might explain why? Is the second hit a low dose?

These have been corrected in the new Fig. 6B.

(11) Given that loss of either TWIK2 or Nlrp3 ablates bacterial protection, a link should be tested - experiments should test whether loss of TWIK2 prevents inflammasome activation in response to ATP (TWIK2 KO in 4E) and if loss of Nlrp3 changes TWIK2 translocation (Nlrp3 KO in at least some experiments of Figures 2/3).

We have now added the TWIK KO results (new Fig. 5E).

(12) One of the most striking data pieces is Figure 1D. It would, therefore, strengthen the paper to repeat those experiments (even just with the high-dose ATP) using TEIK2/P2X7/NLRP3 KO mice and really show the importance of these pathways in vivo. This is conceptually Figure 5, but the survival data of Figure 1 is far more convincing than the relatively weak bacterial load data of Figure 5.

Unfortunately, our previous laboratory has been closed and we have trouble acquiring enough mice for additional survival data during the transition period. However, the bacterial load data has been adjusted to the same bacterial counts per 5 mg lung tissue instead of per individual sampling, giving a more contextual interpretation of the data.