Caching Behavior of Large Prey by Eurasian Lynx: Quantifying the Anti-Scavenging Benefits

Round 1

Reviewer 1 Report

This manuscript investigates the utility of caching kills using observational data from Eurasian lynx (Lynx lynx): killed roe deer (Capreolus capreolus) carcasses, and a set of two experiments focused on vertebrate and invertebrate scavengers, respectively. I enjoyed reading the manuscript, the analyses/statistics are correct, and the results are clearly presented and discussed, and the manuscript is well-written. I have nevertheless a few comments.

I think that it could be worthwhile to discuss if you observed that caching behaviour varied from one individual or social status to the other. If you have data of individual lynx, did a given individual always cache its kills or in most of the cases, etc…? Could you see a difference between males/females/females with kittens and between social status (i.e. sub-adults/floaters/residents)?

Did lynx cache more their kills when they were located in open habitats compared to dense vegetation? What is the proportion of lynx kills (wild ungulates such as roe deer) found in open vs closed habitats, I am asking to see if the two experimental designs focused on vertebrate and invertebrate scavengers match with the kill sites selected by lynx followed by telemetry (i.e. same proportion of kills in open vs. closed habitats).

Could you observe lynx that were feeding on the kill of another lynx? If yes, how many times did you observe this (frequency)? It is known that adult male feed on the kill of females with kittens, but did you observe it in other situations (e.g. resident females that share a kill)?

It could be worthwhile to have a look at these aspects if your data allow it. Elsewise some of these aspects could be included at the end of the discussion as perspective for future studies. See also my specific comments below.

 

Best wishes

 

Specific comments

Lines 71-87: According to the information provided it looks like that these data are biased towards winter where invertebrate scavengers are absent or if present have a reduced effect If this is the case it could be worth to mention it right away in M&M.

Moreover, carcasses start to decay earlier in summer and hence the smell could attract potential scavengers earlier in summer compared to winter, the carcass being covered or not. Hence, unless your data were collected only during wintertime season could matter as well and should be included as factor in the model selection. Clarify please and adjust if necessary.

Moreover, caching behaviour could vary from one individual to the other? In this regard it could be worthwhile to include lynx individuals as a random factor in the model fitting if this information is available.

All these aspects should be mentioned in M&M and/or discussed.

Lines 88-97: Did you deploy the carcasses in open or closed habitats (e.g. forest)? Specify please.

Line 90: Could you please provide further details on the video equipment (brand, flash type…), setting (video length…) and deployment (distance from the carcass, height from the ground…) used to monitor the carcasses?

Lines 122-124: Could you please add how many kills were inspected in summer and winter? I suspect that the dataset is biased towards winter. Moreover, please add how many different individuals were followed during this survey?

Lines 143-146: This part should be deleted as it repeats what is written at lines 136-139.

Table 3: It is not very clear what the value in brackets stand for. It is the weight of roe deer (parts) belonging to each pair. Moreover, sometimes the values are sorted from least to greatest value and sometimes the other way round. Instead of hyphen I suggest using a slash elsewise it corresponds to a range of values. Clarify please.

A zero appears in the second row of the second column. Is this correct?

Lines 209-214: here you could refer to Wikenros et al. (2012):“We found no evidence of cleptoparasitism by wolves on roe deer killed by lynx.”

 

References cited in my review

Wikenros C, Liberg O, Sand H, Andren H. 2010 Competition between recolonizing wolves and resident lynx in Sweden. Can. J. Zool. 88, 271–279. (doi:10.1139/Z09-143)

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

It is intersting and well written paper. Worth to publish in its current form.

Author Response

We are very grateful for the encouraging evaluation.

Thank you very much for your kind attention.

Reviewer 3 Report

This is a very interesting and well written manuscript. However, I think both the description of the analyses and the reporting of results could be improved, with relatively minimal effort.

As stated above, I think the results and models could be much better explained. Now all candidate models are presumably listed in an Appendix that have not been provided. In addition, there are no criteria in the manuscript for how the most adequate models were selected from the candidate sets, despite a rich literature suggesting that based on delta AIC values alone, several models may have approximately equal empirical support (Burnham and Anderson has alternated the threshold for this support from 2 [Model Selection and Multimodel Inference 2002] to 7 [Burnham, Anderson & Huyvaert 2011 Behav Ecol Sociobiol 65:23-35]. In fact, since some contrasts are clearly defined a-priori, e.g. treatment, I would recommend the authors to abandon this AIC based approach altogether. From what I can read from the MS there are only two predictors for the model based on the observational data (treatment and time, lines 85-87, although I think an interaction should be included) and three for the deployed carcasses (treatment, season and treatment x season). With so few predictors, and with some explicitly linked to a-priori defined hypotheses (i.e. treatment), I think simply evaluating model terms in a sequential manner will be more informative and clear, i.e. report results from the two-way interactions, and if those are not significant main effects, or if they are significant, contrasts within interactions. That way the information in Appendix A would be totally superfluous, and there fill also be a statistical results for the predictors of concern (e..g now we are missing results for the effect of treatment on mammalian scavengers in the placement experiment, Table 2a)

I also noted an imbalance in the reporting of the results. Now, results from the observations are given in a (largely uninformative) table, the results from the placed carcasses in a table and a figure, and the results from the invertebrate experiment also in a table and a figure. For the two latter, there is a fair amount of overlap between the tables and figures in terms of information. I would therefore recommend to introduce a figure with results also for the observations, and remove table 1-3 and report this information directly in the text instead. That way each result would be reported as a figure and in the text, which is much more coherent and also without duplication of information.

Minor comments:
Line 42: “energetic” what? Should this be “energetics” or “metabolic rates”

Line 55: Either “an investigation” or “investigations”

Line 65: rewrite to “...extensive boreal forests with relatively low human...”

Line 82: “which range of factors” What factors? From what I can see (lines 85-87) it is only two, treatment and time. Please clarify

Line 84: I am a bit confused over how Akaike weights were used for model selection. These are usually used to eight model contributions to specific parameters in situations of model averaging. I could not find information about any model averaging in this manuscript, so I am not sure in what context the AIC weights were used. I don’t think they can be used for model selection, since they are derived directly from the relative AIC values, and do not hold additional information to those.

Line 85-87: Was no interaction between time and treatment included? Why not? Should be justified.

Table 1 and 2: These hold very little information. The intercepts are not informative, so these tables only presents 2 (Table 11) and 1 (Table 2a and b2) parameters, respectively. I think could more efficiently be reported directly in the text, especially since there are some overlap in information between Table 2 and figure 1. Instead, I think it would be informative to include tables outlining the candidate models, which now have been put into an appendix (which, by the way, is not included in the the review files).

Table 2: If kept (although see my comments above), replace “intercept” with “summer” and “covered”. Also, I assume these are the direct parameter values on a logit scale, in which case the interpretations of the intercepts and the second parameters are very different (i.e. the intercept is the estimated mean logit probability and the second parameter is the difference between the mean of this factor level and the intercept). Perhaps this should be explained if the table is kept as it is, or the table should report predicted averages for each factor level instead?

Table 3 and figure 2: These is a fair amount of duplication here. I would recommend to remove the table, see my general recommendations above.

Lines 185-187: I am a bit uncomfortable the way this sentence is written. Perhaps alter it to something like “The results from the video-monitoring suggested that covering was efficient for deterring avian, but not mammal, scavengers.”

Appendix A: As indicated before, Appendix A is missing

Supplementary files: Tables S1-S3 are not mentioned in the manuscript.

Author Response

Please see attachment.

Author Response File: Author Response.docx