In this manuscript, the authors use avian malaria as a model system to explore and contrast individual- and community-level drivers of infection. The framing of the study is sound and the dataset from the Thousand Island Lake system is impressive. My major criticisms involve the use of avian malaria as a model system here and some of the downstream statistical analyses at the individual- and community-level scales. Given these concerns, I am a bit cautious to read too much into the Discussion, as I expect key results may change somewhat. These concerns are outlined below with more minor line edits.

1. I think the authors have done a generally nice job justifying the study and the need to assess infection risk at diverse biological scales. However, the introduction to the avian malaria system (L90-101) is quite sparse and doesn’t do much to justify the use of this study system. Although avian malaria is commonly described as an important model system for ecological and evolutionary questions, I think the authors need to better integrate some of that literature and provide more background on the system (e.g., transmission, virulence, host range, etc).

2. Similarly, the authors offer no predictions at the end of their Introduction, which makes the analyses seem more exploratory than I think they actually are. It would be beneficial to see predictions both about the individual/community drivers of infection risk as well as about which traits you expect to see convergent patterns across scales (if any).

3. Some critical details on sampling are missing that inform the downstream analyses. Birds were sampled from 2019 to 2021, across 30 sites. How regular/seasonal was sampling? Were all sites sampled at similar intervals, or is there possible confounding between season, year, and habitat? How generally are the ~30 bird species distributed across these sites (e.g., are most bird species found in all sites, or is there substantial filtering of the avian communities)?

4. The authors include individual- and species-level traits. For individual-level traits, several measures seem redundant (e.g., both tarsus and wing length are structural measures of size and should be positively correlated). What about other individual traits of avian hosts, such as age, reproductive status, and fat score? The latter is likely more informative than the BCI for truly capturing body condition.

5. The Bayesian hierarchical model used in section 2.5 is robust but is likely improperly specified, at least at the level of individual infection status. The authors are likely missing a random effect of bird species independent of phylogeny, which accounts for the repeat measure nature of individuals nested within species. See Cinar et al. 2022 MEE for a careful analysis of why both species and phylogeny are necessary to include, as long as the average correlation among species (e.g., from your phylogenetic correlation matrix) is greater than 0.2. The authors should assess the mean correlation from their phylogenetic correlation matrix (excluding the diagonal) and, depending on the observed value, adopt the more parameter-rich (but necessary) PGLMM random effects structure.

6. The authors use a stepwise (backwards) selection strategy in both their individual-level and community-level analysis (L247-253). This has been widely acknowledged to be a biased and poor strategy of model comparison/simplification (see Whittingham et al. 2006 JAE for the most thorough argument, although calls for careful, a priori model specification were also outlined earlier by Burnham and Anderson’s 2002 text). Rather than removing “non-significant terms” (itself discouraged in Bayesian modeling), the authors should specify an a priori set of biologically meaningful models to compare with DIC or LOOIC; outlining predictions earlier in the Introduction could help here. For the individual-level analysis, the authors have a very large sample size, so it should be possible to derive a set of models that are “as full as possible” but exclude collinear terms, and then compare among a reasonable set of models that include relevant combinations of those collinear terms (e.g., if A and B are collinear, one model might have all terms + A while another has all terms + B). Note, however, that this strategy will not work for the community-level analysis, where you have 30 communities (so a “full” model with 7-8 coefficients will be dramatically overfit). For 2.5.2, the authors should parameterize their model with sample size in mind to avoid overfitting (while also limiting comparing more models than the authors have data). In general, a more biology- and data-driven model comparison strategy seems warranted.

Line edits:

L52: The authors may also consider citing Plowright et al. 2017 Nature Reviews Micro as a good overview of the hierarchical infection process.

L91 and elsewhere: The parasite genus is Haemoproteus (rather than Haemoprotesus).

L150: The authors should include a citation for HWI as a measure of dispersal ability.

L152: The authors should cite the IUCN here for habitat specificity.

L154: It is unclear where the authors are deriving migration data, as AVONET derives migration strategy as resident, partially migratory, and migratory. Winter and summer migrant are also unclear terms in the avian literature.

L165: Note that applying PCA on species-level data can be problematic due to the shared correlation among traits for closely related species. In such cases, a phylogenetic PCA is preferable for more robust axes of variation (see Revell 2009 Evolution and phytools in R).

L181: There is some support for the idea of simply selecting the most parameter-rich model when building phylogenies (see Abadi et al. 2019 Nature Communications). How sensitive is the topology of your haemosporidian phylogeny to the evolutionary model used?

L189: Note that the analyses described below focus on the individual level and community level only, rather than also having a species-level analysis.

L191: I would qualify this as “relatively robust estimation of prevalence”, as n = 10 is still rather small for estimating a proportion.

L195: It would be more accurate to refer to the model more simply as a phylogenetic generalized linear mixed model (PGLMM), as the Clark et al. paper cited here did not originate this model type.

L219: I think the authors can remove the hyperlink and simply cite the brms package and associated manuscript by Bürkner (Bürkner 2017 JSS).

L224: It would help here to remind the reader that this is a binomial GLM. Adopting PGLMM language for section 2.5.1 as suggested above would better help make this transition/clarification.

L253: The authors should consider reporting R2 for brms models.

L340 and elsewhere: The authors oscillate a bit between “pathogen” and “parasite”; both are appropriate for the avian malaria system, so it would be best to pick one for consistent use.

L343: I would caution against reading too into implications of the results for tolerance, given that the authors are only measuring the probability of infection (and not intensity).

Figure 3 and 4: It would be helpful for the figure legend to define the intercept of the brms value so that the reference levels for categorical terms are clear.