Engskog-Vlachos et. al investigate microglia metabolic adaptations to in vitro stimulation with LPS and IL-4 in BV2 microglia. The scientific background of the work is solid, and the approaches used are advanced related to metabolic profiling and siRNA knockdown. The findings related to LPS and IL-4 stimulated BV2 microglia support prior studies, and the identification of itaconate as an immunometabolite regulating NRF2 activation in microglia is novel and may be important for in vivo studies. The manuscript is well written, and overall, the findings are well contextualized within the literature. Nonetheless, there are some points that require the attention of the authors.

Major:
Figure 3 - Have the authors investigated whether the increase in malate levels are derived from increased mitochondrial or cytosolic compartments? This could provide additional mechanisms to support the metabolic changes observed in response to LPS; mainly related to malate-aspartate shuttling, and cytosolic malic enzyme.

Figures 4, 6 - Authors may need to reassess the OCR data. Maximal respiratory capacity of LPS treated samples is below the baseline respiration, which could suggest that there may be technical limitations to this specific experiment. This could be due to inadequate concentrations of oligomycin leading to mitochondrial damage, or inadequate concentration of the uncoupler. Authors should try to titrate FCCP or oligomycin concentrations to optimize response on the LPS treated samples whilst retaining the uncoupling effect on the other two groups.

The authors suggest that the effects of LPS and IL4 on inflammatory response (NOS2 and ARG1), and on metabolism (NRF2 and IRG1) peak at 6h, and based on the western blot results, they only seem to manifest after 2-3 hours. Yet the response of the BV2 cells to LPS injection seems to be immediate. Why have the authors not pre-stimulated the cells for the 6h with LPS or IL4, and then performed the Seahorse? Also, could the authors explain why the “pro-glycolytic” effects of LPS far precede the changes to itaconate synthesis?

Figure 5 E-G - On the RT-qPCR analysis of siRNA transfected BV2 microglia, am I mistaken to interpret that the results show that silencing Acod1 does not affect NRF2 levels? Wouldn't that suggest that Itaconate synthesis (Acod1) is not transcriptionally regulating NRF2? This result is confusing, as it doesn’t align with the already described itaconate-NRF2 regulating pathway.

Minor:
Figure 1A - in line 113 authors mention that the response to both LPS and IL4 reach their maximum at 6 hours of stimulation. There is extensive literature using BV2 cells with longer stimulation periods (e.g. 12h, 24h). Further, authors only present results with stimulation up to 6 hours, therefore there is not data here to support that additional stimulation will not lead to increased response. Authors may opt by rephrasing this sentence to appropriately describe their findings.

Figure 1B. - Samples used for the metabolomic analysis are described as 10 technical replicates. Are these 10 independent experiments or 10 wells per condition of the same experiment. If the latter is the case additional independent experiments would be needed to provide more confidence in the results.

Figure 1D-E - The manuscript lacks a description of the PCA analysis on the methods section. Additionally, what was the method used for defining the clusters on the PCA biplot? There is a clear distinction between CTRL and LPS based on PC1, but there is a lot of overlap between CTRL and IL-4 on the PCA. I wonder if these are genuinely distinct signatures, or a pseudocluster based on biased cluster analysis.

Figure 2 - The description of the three types of feature regulations on line 164-166 is not very clear, and difficult to follow. It only becomes clear what the different regulation types mean once the authors present the results. Maybe authors can rephrase this section to improve clarity.

The limitation of sole relying on BV2 cells for these studies should be discussed. Can these findings be related to primary microglial or hIPSC microglia studies, or similar studies in in vivo model systems? I appreciate that models are required for this type of metabolomic approaches, but how the findings translate to other systems is in doubt.

The manuscript should be carefully proofread/copy edited prior to resubmission.

The authors address my comments fully. Thank you.