I read this paper with great interest. The experiments appear well-designed and the study addresses two major aspects in the disease ecology of white-nose syndrome – what is the impact of different hibernation temperatures and variation in inoculation loads on disease outcomes?
However, I am deeply puzzled by the results. The paper shows that only one treatment group had higher mortality than the control group – the 500 spore/conidia group - whereas groups inoculated with 10 to 10,000 times more conidia (5000 to 500,000) had survival that didn’t differ significantly from the control group. This suggests that there was little WNS mortality in the experiment, and that disease effects (e.g. the increased arousal frequencies of infected bats compared to controls) were sub-lethal. However, the authors argue that the mortality in the 500 conidia group was due to WNS, despite not seeing any significant mortality in groups inoculated with higher loads. This is puzzling because the fungal loads on bats at the end of hibernation parallel the inoculation loads. In addition, only 5 of the 30 bats infected with 500 conidia at the two treatment temperatures had any detectable conidia at all at the end of hibernation. Despite this, the paper argues that the bats in the 500 conidia group that died, did, in fact, die of white-nose syndrome. I can’t see how this conclusion can be reached since <20% bats had any detectable conidia on them, and other groups had much more fungus on them, but no significant mortality. The paper argues that the increased arousal rates of the 500 conidia group demonstrate that they were in fact affected by the fungus in a way that is consistent with WNS. I find it difficult to understand how one can attribute the deaths in the 500 conidia group to WNS when >80% of these bats had no detectable fungus. Previous papers suggest that nearly all bats dying from WNS have clear infections by histopathology (e.g. Blehert et al 2008 Science), and recent presentations at WNS conferences where authors from this study were present suggest that infection loads on bats in the field at the end of hibernation are very high. Thus it seems very puzzling to assert that bats could die from WNS but have no detectable conidia.
The suggestion that bats were somehow controlling the fungus so it was undetectable and yet dying from WNS seems contradictory to me. In general, there seems to be a contradiction between the inoculation dose and end-of-hibernation infection intensity data which showed parallel and consistent patterns, and the inoculation dose and mortality data which showed a contradictory pattern. The lower mortality for higher infection intensities also contradicts most other experimental infection studies I am aware of that include a range of pathogens such as fungi, viruses, protists and bacteria and a range of hosts including mammals, birds, and amphibians. Is it possible that something else caused the 500 conidia treatment group to have higher mortality and higher arousal frequency that had little to do with WNS or fungal infection? This seems potentially more parsimonious than the explanations given in the paper. Perhaps the authors could comment on something else that might have differed between this group and the other infection groups?
Finally, the authors discuss a previous study (Lorch et al 2011 Nature) in which there was no significant mortality compared to control bats after a 500,000 conidia inoculation, and argue that this could be due to the large inoculation dose and density-dependent growth of the fungus. However, the idea of density-dependent growth is contradictory to the loads the authors measured on bats at the end of the experiment which showed a highly significant increase with inoculation dose. In addition, another laboratory experimental infection study that used the same 500,000 conidia inoculation dose as Lorch et al (Warnecke et al 2012 PNAS) had highly significant mortality after 70-115 days with the timing of mortality depending on the strain of fungus used. Thus, the lack of mortality in the Johnson et al study with a 500,000 conidia inoculation dose over a 150 day period cannot be attributed to density dependent fungal growth and a 500,000 conidia inoculation dose is not a suitable explanation for the lack of mortality seen in the Lorch study and the current study. Instead other factors are clearly at play, and it would be very useful for the scientific community if the authors could comment on other potential factors that might have produced the results they observed.