I would like to thank the authors for the opportunity to review their manuscript investigating the interactive effects of mercury contamination on infection with influenza A viruses (IAVs) in waterfowl. Very few studies have examined the infection-level outcomes of toxicant immunosuppression, especially in wildlife, making this a unique and valuable contribution to our understanding of the broader drivers of infectious diseases in wildlife and potentially spillover to other animal and human populations.
The authors used GLMs to assess potential correlations between active IAV infection (detected by PCR) or antibodies to IAV (detected using ELISA on serum) and a key environmental pollutant – Methylmercury – whilst taking several temporal, demographic, phylogenetic and physiological covariates into account. They also used GLMs and GAMs to assess whether IAV infection may have a negative impact on body condition (using demographically-adjusted crude fat percentage as a proxy for body condition) and whether these effects would be exacerbated by mercury contamination.
Overall, the paper is technically well written, well structured and very easy to follow. The concepts presented in the ms and the data that underpin it both have considerable merit and could spur substantial follow-up research into toxicant-infection-transmission relationships in wildlife. However, there are several major issues with the manuscript in its current form.
First, the results are oversold. The results clearly state no effects for models assessing active infection: (L268-272) “Our ecological predictors explained very little of the variation in active infection status; the full model had an R2 of only 0.08, there was no strong evidence for an effect of any variable in the averaged model, and the intercept-only model was competitive (ΔAICc=1.490, Table S3), indicating that the other parameters were uninformative [67]. The only variables with positive relative importance scores were age and the interaction between age and date (Table S4)”. Yet, in direct contradiction of these findings, the abstract states (L9-10) “the probability of active influenza infection also increased with blood mercury concentrations” and the discussion states (L287-289) “we found a positive relationship between the probability of influenza infection and blood mercury concentrations”; (L327-328) “the positive relationships between influenza infection probabilities and mercury concentrations” and (L311-312) “compelling evidence that the immunotoxic effects of mercury might increase the prevalence of influenza infection across waterfowl host species”. In defence of the discussion the authors may argue that they refer to their more significant, though barely more predictive (R2 = 0.08-0.11) analyses of factors correlated with the presence of antibodies, but the language appears wilfully misleading. Even the title “Avian influenza prevalence increases with mercury contamination…” is misleading, given that avian influenza prevalence would be widely assumed to refer to prevalence of active infection, not antibody prevalence, and active infection showed no relationship with mercury contamination at the individual or species level.
Secondly, there is a pressing need for mechanistic details about how Methylmercury has been shown to alter immune function in mammals and birds in the literature. Does exposure to this toxicant reduce a host’s capacity to detect pathogens? Proliferate innate immune responses? Develop antibodies to novel pathogens (time taken, sensitivity or specificity)? Maintain antibodies or immune memory? These mechanistic details, from the literature, are essential to interpreting the results presented here. The immune system is not a single lever – both reduced susceptibility to infection and increased competence once infected, which coalesce to influence transmission and prevalence in a population, are, for IAV, largely dependent on adaptive immune responses. And so, if there is evidence to suggest that aspects of the adaptive immune response are impaired, this has major implications for the use of detectable antibodies as a proxy for prior infection. At its extreme, immunotoxicity that prevents antibody production could indeed result in individuals being more susceptible to infection, yet you would not know they had been infected, because the measure of prior infection is detection of antibodies using the anti-NP ELISA. This is critically lacking in the conceptual framework throughout the paper, as illustrated in Figure 1 – where immunotoxiciy and immune responses to IAV are presented as completely separate. Part of the mechanistic details needed are relevant toxicant concentrations. Although the discussion notes (L340-341) “mercury concentrations in most birds we studied were below benchmarks expected to affect animal health [4]”, it is essential to add quantitative information to this – what concentrations have been shown to have effects in previous studies? Can these be indicated in the figures? Also, how relevant are blood concentrations, vs the other organs that were sampled (but no data presented)?
Importantly, the data from this study has the potential to contribute mechanistic insights as well. For instance, although often reported as a binary, qPCR analyses for active infection also provide quantitative information on viral load (Ct values). For instance, Ct values could be used to investigate whether mercury contamination may increase competence for infection. Although previous infection may muddy this relationship in adults, most juveniles would be experiencing infection for the first time, so analysing the effect of Hg on Ct in juveniles (together with appropriate covariates) could provide unique information on the relationship between mercury contamination and competence for infection. Likewise, relationship between active infection and detectable antibodies could provide valuable insights into the role of Hg in supressing seroconversion, especially in juvenile birds who will be seroconverting for the first time. While there will always be infected individuals that are yet to seroconvert, if there is a suppression of seroconversion and/or an extended period of infection as a result of Hg exposure, you would expect individuals that have high Hg concentrations to be overrepresented in the PCR+/AB- category and underrepresented in the PCR+/AB+ category.
My third major issue is with interpretation of detectable antibodies as an indicator of prior infection. While it is undeniable that an individual with detectable antibodies has been infected (with the exception of maternally transferred antibodies to IAV – in mallards this only lasts ~6 weeks), a lack of antibodies does not mean that an individual has not been infected recently. Presence of antibodies in an individual is dependent on a number of factors, including time since infection, number of previous infections, likelihood of seroconverting after infection (which can differ substantially between species, and age groups), duration of antibody persistence (which also differs substantially between species and age groups), and others (see Gilbert et al 2013 'Deciphering Serology to Understand the Ecology of Infectious Diseases in Wildlife', EcoHealth, 10: 298-313). Even in experimental studies, with their limited sample sizes, have shown that not all waterfowl have detectable anti-NP antibodies after infection. Because most of these variables are not know, comparisons between species are not recommended. Comparisons within species, for the species for which there are a reasonable number of samples (per time point, per year, per age, per sex) can be made. Moreover, because toxicant exposure may theoretically alter time since infection, number of previous infections, likelihood of seroconverting after infection, duration of antibody persistence etc, relationship between mercury concentration and presence of antibodies may show complex relationships that cannot be teased apart in cross-sectional data. While I do not expect the authors to be able to tease these apart, the antibody data must always be referred to as “detectable antibodies from prior infection” (or detectable antibodies) rather than “prior infection” and the interpretation of these results must reflect the major caveats to the use of serology in the type of study presented.
It’s also important to keep in mind that over the course of the winter sampling period, almost all individuals in many species are likely to have been infected given the prevalence of active infection and the known duration of active infection. While the authors’ arguments about the distinction between short- and long-term risks may hold true in other disease systems, they may not hold in a system where almost everyone is infected over the course of the sampling period (i.e. long-term risk is the same for most). Moreover, there are issues with temporal correlations – IAV infection occurs throughout winter such that most juveniles, although naïve in autumn, will have been infected by spring. I would assume (but could be wrong) that mercury contamination is also more likely on wintering grounds than on Arctic breeding grounds of these ducks, meaning that you would expect mercury contamination to increase over the winter (which is suggested by the maximum concentration of mercury in Figure 3), meaning that you would find a correlation between probability of antibodies (but not active infection) and mercury concentration because of two separate causal relationships with time, rather than causal relationship between contamination and infection. Together, these alternative interpretations suggest the need for more nuanced analyses and interpretation of sections of the data, in relation to the biology of the system, rather than blanket GLMs and model averaging for a single solution.

Minor comments
1) If body fat has already been standardised by species and age/sex, it seems inappropriate to (re)use these variables as predictor variables to assess differences in body fat %, or to include both the derived variable (body fat %, adjusted for species age and sex) and species age and sex in models assessing variation in IAV infection/antibodies. Biologically, I can see the desire to partition the influence of age or sex on infection from the influence of body condition on infection, but I’m not sure this is a statistically valid approach.
2) Analyses using species as a fixed effect need to account from the phylogenetic relationships between the species, because their phylogenetic relatedness means that all species are not equally independent from one another.
3) The term “prevalence” is used both in relation to number of infected individuals within a population and in describing an individual animal’s probability of infection, especially in relation to Mercury. While the first is spot-on, the second is inappropriate. E.g. L12 ‘incidence of influenza virus’ rather than ‘influenza prevalence’, because your data are about individual probability of infection, not population level (i.e. prevalence). Likewise L57 the rest of the sentence implies individual-level effects, in which case ‘infection risk’ or ‘likelihood of infection’ are more appropriate than ‘infection prevalence’ (a population parameter). Similar instances throughout the ms – e.g. L162, L295, L308, L363.
4) There is considerable replication (direct copy) of sections of the methods section in the supplement, which is unnecessary. Simple, repeatable methods need to be in the ms, and additional details of specific steps (e.g. those already published elsewhere) can be included in the supplement.
L47 ‘resistance and tolerance’ rather than only ‘tolerance’, because immune responses, and toxicant clearance, are resistance mechanisms.
L53 there is no ‘direct transmission’ route for influenza viruses in wild birds. Transmission generally via the fecal-oral route (i.e. indirect via water vehicle), which can be immediately after defecation or some time thereafter. Although ferrets and other animal models have been shown to transmit IAVs by aerosols, I am not aware of any such studies in wildlife.
L108 “Ducks were collected” – how were ducks captured or collected? Given the cardiac venepuncture method and the hunting organisations in the acknowledgements, I presume these are hunted ducks, but that information needs to be detailed in the ms, including time from being shot to collection. In addition, in my experience, blood from venepuncture of dead waterfowl, even within one minute of being shot, is lysed, such that any plasma or serum fraction is contaminated with internal fluid from lysed RBCs. Lysed samples are not reliable in anti-NP antibody ELISAs. Can the authors comment on the condition of the blood collected and whether lysis was scored prior to ELISA?
L133-135 “All rRT-PCR-positive samples tested negative for highly pathogenic clade 2.3.4.4 viruses [58] and thus were inferred to represent infection with low pathogenic influenza viruses.” HP clade 2.3.4.4 is just one HA segment with HP characteristics. Many other H5 Has and other HA types (7, 9, …) have HP forms. You can therefore only conclude no HP H5 clade 2.3.4.4 was present.
Table 1 – 95% CI of antibody prevalence and active infection prevalence needed
Figure 2 - It appears that variance is not homogeneous across species in both mercury concentration (noting that the x-axis error bars are equal left and right, despite the log scale of the x-axis)
Figure 3 and text reporting odds ratios - 85% CI are used throughout, with the standard 95% CI included in the 95 pages of supplementary material. I’ve never seen 85% Cis used, and it seems an explanation for this is needed in the ms. Notably, many of the 85% Cis reported for OR in the text are very close to overlapping 1, suggesting that 95% CIs would be either side of 1, implying no significant effect.
Figure 3 – labels for the date panels currently imply that the data are from a single day of sampling. It would be more appropriate to label these with “early-“, “mid-“ and “late-winter”, with an explanation of how the periods were determined indicated in the figure legend.

The authors have greatly improved the manuscript in line with comments from all three reviewers. For the most part, all of my comments have been directly addressed. I only have a few minor comments:
L133-135 needs to qualify H5 Highly pathogenic clade, as the clade is within HA type.
L 208&209 needs to be part of the previous paragraph (rather than single sentence paragraph)
L264-265 In light of the low R2 (0.08-0.11) and the high p-value (p=0.089), I'd suggest the authors insert a "weakly but" in between "infection is" and "positively associated" in the sentence "Together, these patterns suggest prior infection is positively associated with blood mercury concentrations both within and across species."
Similarly, the opening paragraph of the discussion is still phrased in a way that implies strong, significant, predictive relationships were observed, which isn't the cae.
L271 "Prediction lines for 16 Oct, 1 Jan, and 16 Mar" needs updating to match the more general headings within the figure
L282-285 given these results are so weak, and not strongly supported, it would be better to state "infection probabilities tended to increase with blood mercury concentrations" rather than "increased", and "adults tended to be less likely to be infected than juveniles" rather than "were" etc