Manuscript ID: ESO-21-08-083
Review By: Matthew Stuber, U.S. Fish and Wildlife Service
Review Date: 01/17/22

I appreciate the opportunity to provide a review of this manuscript revision. I think the information presented in this paper is important to make public. It will certainly add to the scant body of information discussing the effectiveness of automated curtailment. Thanks to the author’s for their detailed responses to my initial comments, and for addressing many of them in this revision. I think it is an improved manuscript. There are only a couple of concerns of mine that were not addressed, and they were some of my biggest concerns. These concerns were are:
1. The longevity of the “After” period. One year of “After” data severely limits the author’s ability to infer that the reduction in fatality rates can be attributed to the treatment. I understand why such additional information was not added here – because it would likely take years to collect that information. However, the absence of this information still severely limits the ability to claim that any observed reduction in fatality rates were a direct cause of the treatment. See Comment 1 below for more detail.
2. The absence of details on the treatment (i.e. the programming of the Identiflight system). I appreciate the added reference to other papers, but a quick glance at the cited works does not seem to answer the question “when was a turbine curtailment ordered in this study?”. I acknowledge and appreciate that the author did add language that indicates the programming of Identiflight can vary and may influence its effectiveness. But to omit the details of such programming in this manuscript seems akin to studying the effectiveness of a prescription drug, but then not mentioning what dose was studied. I think that such information is essential, otherwise it further limits the usability of the paper, and one’s ability to infer outside of the confines of the treatment site.
3. I still think that more discussion is needed on the limitations of the findings. See Comment 2 below for more detail.
Comment 1: I see the authors took my advice to take a closer look at annual variation in fatality rates during the “Before” years. However, the look at that data seems to reinforce a concern I had, that the reduced fatality rate at the treatment site in the “After” year would not have been unexpected due to chance, and not necessarily a result of the treatment. Exact fatality rates are not given, but the difference between fatality rates between 2015 and 2017 (both pre-treatment years) appears to be about 7 (9 -2 = 7 eagles per year). The difference between 2017 (pre-treatment) and 2019 (post-treatment) looks about the same at 8 eagles per year (9-1 = 8). Of course, I’m just eying this up from Figure 2b, so exact numbers may be a little different. But without considering the data at the control site the reduction at the treatment site after treatment does not appear out of the ordinary. Therefore, to me the only bit of evidence left to help make the case that the observed reduction was a result of the treatment is the comparison with the control site.
There IS some compelling evidence in this comparison. First of all, the comparison between sites does seem to suggest that the fatality rates at the two sites fluctuate with each other in some years, with the possible exception of 2017. So I agree with the authors that these sites do not seem to be inappropriate to compare. And it is exciting to see, in the year post-treatment that the fatality rates dropped at the treatment site, but not at the control site. That DOES seem to suggest that there may have been some impact from the treatment. However, as the data from 2017 indicate, fatality rates are probably not going to be in lock-step with each other every year. Because of this, and because only one year of data exists post-treatment, it brings back my concern that it might just be annual variation that is at play here, and not an actual treatment effect. Addition of additional years of study would be very helpful in alleviating this concern.
Comment 2: I think that the inference of this study should be clearly limited to a) the treatment site and b) the way the Identiflight system was programmed. Further, I think even more discussion is necessary on the limitations that come from only one year of post-treatment study at only one site . These are extremely important caveats to include in this paper, because otherwise I fear it will be tempting for readers to assume that just because Identiflight is installed at the treatment site, it will have similar effects at other sites in other years and under other programming. The author’s have done some work since the first manuscript I read to highlight the limitations of the inference, which I appreciate. But in my opinion it is still not enough.
To be clear, I believe it not only incumbent on the author to make such limitations clear in their write-ups, but it is also incumbent on the reader/user of the research to understand those limitations. So this shouldn’t be all on the author to discuss. However, as a user of this science, and someone who works with users of this science, I can tell you that extra care and explanation might be prudent here.
In an illustration of this, the Senior Vice President at Identiflight recently was quoted, when speaking about the results of McClure et al. (2021b) “We now have conclusive evidence that Identiflight can be utilized as a mitigation and minimization solution for current and future wind projects.”. I see that as an exaggeration of the findings of this study, which are based on only one year of post-treatment study, at one project, and under only one curtailment regime. Yet, this is what Identiflight is likely telling all of their potential buyers. At least its what’s on their website.
Of course, exaggerations on a company’s website doesn’t bother me. They are trying to sell a product after all. But I believe that limitations should be made clear in any peer-reviewed publication.