This is an interesting study, asking a relevant question. I appreciate the geographic span of the sampling sites, which makes it relatively unique – analysis of 5 native and 4 non-native populations appears generally trustworthy and promising. The article is well written, though in my opinion the Methods are too brief (see below) and the Discussion a bit too long given the results obtained. My major issue is the interpretation of the results which seems to neglect the possibility of simple mechanisms in immune regulation that can lead to similar patterns in the results (again, see below). In my opinion the problematic points need to be clarified before the article can be published (please see the Comments to the Authors).

Major points:

1) The gene expression study was performed in blood, but this was not compared to any tissue. Not even the introduction, methods or discussion mention any comparison of blood gene expression with tissues. During immune response, there are important differences between the tissues in cytokine expression levels (Vinkler et al. 2018). Blood is a transportation medium, but typically not a site of infection. The cells in blood are not activated in their natural context of the infection site and, therefore, the levels of blood gene expression can be biased compared to the actual sites of infection (here mimicked by the LPS application). The manuscript does not mention any evidence of association of the gene expression levels in blood and tissues that would evidence that the blood levels are relevant for the protection. The authors claim that they have also liver, spleen, and gut samples collected from the birds available – can any such association be shown?
2) The methods are very brief and lacking much of the detail that are needed to judge reliability of the approaches taken. Especially, if new expression primers and probes were designed in this study (as suggested in the Methods, line 167) then the authors have to evidence functionality of their assays – namely show efficiency of the PCR. There may be also DNA polymorphism in the sparrows (e.g. differentiating the populations) that interferes with the PCR (SNPs at the positions of the primers), biasing the results. The reader needs to be convinced that this is not the issue. Furthermore, were the absolute copy numbers compared during the assay design to any relative gene expression data using a reference gene / genes? What I miss the most is any indication of the reliability of the measurement - the repeatability. I understand the technique, but I miss data validation, which is an issue when a new assay is being introduced.
3) Disussion: I am a bit uncertain about the interpretation of the results obtained. The study showed negative association of TLR4 expression with the relative change of IL1b and IL10 expression, but only in non-native populations. This is interesting. However, in the manuscript it is interpreted as the evolutionary difference between the native and non-native populations. Yet, if the non-native sparrows suffered more from sub-clinical mild infections (possible), this would increase the TLR4 levels and also IL1b and IL10 levels before the actual LPS stimulation. Then any additional experimental stimulation with LPS would have lower affect in these birds than in the native sparrows (leading to lower change in expression). Is this correct? The statistical result would be the same, but the interpretation would be different. Thus, the result can be interpreted in immunological terms alone, without any evolutionary effects. The authors need either to convince the reader that this (most parsimonious) explanation (i.e. that TLR4 levels are part of immune activation, not adaptation) is not valid or mention this interpretation as one of the possibilities. Were the initial TLR4 levels anyhow related to the baseline IL1b levels? Actually, this possibility goes well with the explanation provided at lines 285-300. Heterophils do not have to respond only to stress, but also to mild infections.

Minor comments:
1. Line 147: what was the number of individuals per population? This information is missing in the text of the Methods, in Figure 1 and Supplementary Table 1.
2. Lines 149-150: “wing cord (to 150 mm)” – is this wing cord, not wing chord? And the accuracy of the measurement is to 150 mm? This seems very strange - the accuracy should be e.g. to 1 mm. Please check.
3. Line 172-176 the authors do not provide any information about the concentration and quality of the RNA extracted – what was the range of the RIN values obtained for the RNA samples?
4. Line 196: was the year of the data collection anyhow considered in the statistics? Were there any populations repeatedly sampled? Did the gene expression patterns varied between the years for these populations? Such information could support the repeatability of your results regarding the estimates for the populations.
5. Results: line 207: the authors first need to evidence that the levels of IL1b and IL10 expression before stimulation did not significantly differ between the populations and ideally not even varied between the individuals. Levels of these cytokines before stimulation can reflect the infection status (the birds were directly collected from the wild) and thus also the ongoing immune responses that could interfere with the immune response to LPS. Passerine TLR4 responds by up-regulation of its expression to immunity activation (Vinkler et al. 2009).
6. Line 215: the endotoxin tolerance part of the Discussion is relatively conceptually unclear. Immune tolerance is a phenomenon of acquired tolerance to the antigen/superantigen. Infection tolerance (Råberg et al. 2007) can be attributed to limited damage caused by the pathogen despite the pathogen loads. Here the adaptation for lower response to LPS is simply adaptive regulation of the intensity of immune responsiveness (Graham et al. 2005).
7. Last but not least, please check the correctness of your references cited – e.g. lines 107 and 137, ref. 13 is Matsuguchi T, Musikacharoen T, Ogawa T, Yoshikai Y. Gene Expressions of Toll-Like Receptor 2, But Not Toll-Like Receptor 4, Is Induced by LPS and Inflammatory Cytokines in Mouse Macrophages. The Journal of Immunology. 2000;165(10). This paper reports results which indicate that TLR2, in contrast to TLR4, can be induced in macrophages in response to bacterial LPS and hence may accelerate the innate immunity against pathogens. However, this study does not show what the authors claim, i.e. that “elevated constitutive TLR expression allows for quick detection and removal of microbes before they inflict harm” (this study did not even perform any infection experiment). Furthermore, the study is in mice, not songbirds. It is critical that the authors adhere to high standards of publication ethics and make sure that throughout the text they provide references supporting precisely the information provided.

References
Graham AL, Allen JE, Read AF (2005) Evolutionary causes and consequences of immunopathology. Annu Rev Ecol Evol Syst 36:373–397. https://doi.org/10.1146/annurev.ecolsys.36.102003.152622
Råberg L, Sim D, Read AF (2007) Disentangling genetic variation for resistance and tolerance to infectious diseases in animals. Science 318:812–814. https://doi.org/10.1126/science.1148526
Vinkler M, Bryjová A, Albrecht T, Bryja J (2009) Identification of the first Toll-like receptor gene in passerine birds: TLR4 orthologue in zebra finch (Taeniopygia guttata). Tissue Antigens 74:32–41. https://doi.org/10.1111/j.1399-0039.2009.01273.x
Vinkler M, Leon AE, Kirkpatrick L, et al (2018) Differing house finch cytokine expression responses to original and evolved isolates of Mycoplasma gallisepticum. Front Immunol 9:13. https://doi.org/10.3389/fimmu.2018.00013