General
In this manuscript, the authors present very interesting data revealing that the green wave hypothesis can partially explain the movements of brown bears, a non-migratory omnivore species. Habitat selection by brown bears in the spring would be determined more by indicators of forage quality than by indicators of forage biomass. Although already demonstrated for black bears, this result is really interesting as it highlights the importance of forage and the ability to track the green wave for another large predator. However, it might be really relevant to evaluate the mechanisms of green wave tracking in brown bears.

I found the manuscript provided some convincing results but also some less convincing results. In the abstract it says “Green wave tracking in brown bears was explained by the spatial transition of green-up, the duration of green-up, and the amount of protein in a bear’s diet”. I was convinced by the approach to the first two points, but for the last point (hypothesis H3) I found the demonstration less convincing. Indeed, the diet was based on the diet compositions reported for each population and sex in the literature. This result is therefore based on a comparison between populations of individuals rather than a comparison at the individual level and is based on knowledge from the literature. We can imagine that there are huge differences between individuals, a variation acknowledged by the authors, so I wondered if it was possible to consider a more convincing approach. In particular, I was surprised not to see a measure of body size or body condition as the authors have repeatedly emphasised the link between individual condition and the abundance of animal protein in the brown bear diet. Also, I am not convinced that the authors can really evaluate their hypothesis H4 of a difference between males and females in the propensity to track the green wave. The sample size of males is very small and out of 7 brown bear populations, 4 populations have no or almost no data! In light of the huge variation between populations and individuals (and then diets), I do not think the authors have the sample size and therefore the statistical power to assess a sexual difference.

My second comment concerns the methodological approach, I was a bit surprised by the RSF approach followed by the authors. I wonder why the authors need to define a homemade home range and why they did not follow a more classical SSF approach.

My final comment concerns the discussion, I found that there is some speculation to find a posteriori consistency in contrasting results. In particular, much of the interpretation relies on the abundance of masting vegetation and animal protein in brown bear diet, but this information is lacking and the effect of the rough estimate of the proportion of animal protein in the diet is not retained for the use of high quality forage and although retained for selection, the effect remains moderate.

I give further comments in the following to go into more detail. I hope the authors will find them useful in improving the MS.

Specific comments
1 (lines 12 and 13) Here and throughout the manuscript, I suggest referring to proxies of forage quality and forage biomass, as the authors do not have direct measurements but only indirect measurements indexing these quantities.

2 (lines 14 and 15) I do not find this sentence really informative as it stands.

3 (lines 25-26) Here and elsewhere, authors stress the maximisation and even optimality of animal behaviour. Here I suggest providing a reference and elsewhere, regarding thoughts of optimality, I suggest moderating this optimality view a bit.

4 (lines 55-56) I am not sure where the authors are going with this sentence, I mean this sentence is so general, this argument does not seem super convincing.

5 (lines 70-74) The link between the forage maturation hypothesis and high energy requirements, in connection with a diet rich in animal protein and masting vegetation, is not obvious. This part is difficult to follow. Moreover, the authors themselves explain that these resources are scarce in spring when the GWH hypothesis is supposed to play a role (see lines 84-85). At least to my understanding, there is something unclear here in the arguments made by the authors.

6 (lines 74-75) Several times in the manuscript, the authors point out that bears consuming more animal protein attain a larger body size which may greatly influence the tendency to follow the green wave. As is clearly stated in the introduction and mentioned several times in the MS, I expected the authors to control for size or body condition in their analyses. At the very least, the authors should explain in the MS why they did not control for body size.

7 (lines 78-79) Again, I find it difficult to understand the connection between the first sentence of this paragraph concerning GWH and masting vegetation. GWH should appear in spring and not in summer or fall.

8 (lines 121-122) It seems to me that it is reversed in the Table 1 compared to the text concerning the mean INDVI. If the productivity is higher, it is explained to be negative in the text but positive in the table.

9 (line 145) This information of 25-91 bears per population is a bit misleading because in the end the authors used between 4-52 bears per population (Table S1). There are 2 populations with very few bears (4 and 9 bears).

10 (lines 146-148) I am really surprised by the low frequency of location acquisition and the low sample size of locations per individual (7257 locations for 182 individuals, an average of 40 locations per individual and spring) for GPS collars. Is it possible to have explanations? Is it possible to know if and how the authors have dealt with incorrect locations?

11 (line 150) Is it possible to know how the authors defined the period of time concerned? Here it is spring, but in the introduction, it was spring and early summer (line 100). I think we have the explanation further on about the beginning of the period with the melting of the snow but we do not know what time period is considered to describe the behavior of bears.

12 (lines 181-194) I am not entirely convinced by the need to define a home range. Firstly, this is a home-made approach, and secondly, I have more the impression that the authors are doing an SSF approach (like Fortin et al. 2005) instead of an RSF approach. Then, I wonder why the authors did not follow the more classical SSF approach by taking 25 random locations from step length and angle distributions (certainly uniform in this case for the distributions of angles) instead of 25 random locations from a home-made home range based on steps and step lengths. Maybe it would not change the results much, but from what I understand, it is more in the rational of assessing whether the bears are following the green wave, as one considers the trajectory, rather than comparing the locations used to random locations in the “full home range”, although I agree that it is a question of scale.

13 (lines 256-262) It is not very convincing to study individual differences on the assumption that individuals behave on average like a population of individuals! As a result, we are not at the individual level as the title of this section suggests. I understand that the authors do not have access to direct dietary information, but as I said before, I wonder why the authors did not consider body size or body condition, either in absolute terms or relative to other individuals in the same population, in order to better capture the variation in diet between individuals.

14 (lines 268-269) What is the distribution of these variables? Is it really Gaussian? The values seem to be between 0 and 1 for the mean IRG, maybe a beta regression would be more appropriate!

15 (lines 271-273) How about considering a single complete model including all variables and taking into account the p-values as is done in the end in this manuscript. I wonder if model selection based on AICc adds much in this manuscript. Moreover, “Contrary to popular opinion, removing variables that are not statistically significant from the analysis may not improve interpretation and may increase the chances of overfitting” from van Smeden (2022).

16 (lines 305-319) The betas are very low! It would be necessary to give effect sizes, here the values are so low that we do not know if it makes sense or not on a biological level! For example, say that when the duration increases by x% (or from minimum to maximum) the dependent variable increases by y% (see also Nakagawa & Cuthill 2007).

17 (lines 318-319) I have a problem with this result. I am not convinced that the authors have sufficient statistical power to assess individual variation. According to Table S1, there are 36 males followed against 146 females and with 3 populations with no males and one population with only one male, and then only 3 populations with 9 to 16 individuals. In light of the strong differences between populations and individuals at least in females, I do not believe that the authors can evaluate and conclude anything supported by the data regarding this point. I can quote van Smeden (2022) again: “While many readers are quick to point out that a statistically significant effect does not mean the effect is also large enough to be relevant, it seems easier to forget that effects that are not statistically significant may not carry strong evidence that the effect does not exist”. The second part of this sentence is really important in this context. I do not think that the authors have the possibility to evaluate their hypothesis H4.

18 (lines 327-328) Same remark as the previous one concerning the relevance of the lack of evidence of the effect of individual variation.

19 (lines 360-361) I strongly suggest keeping the same name for all variables, e.g. spring scale or green up duration, but everywhere. It is not that easy to manage all the variables and it becomes more difficult if the names change over time. Also, I may be wrong but in the 360 line I would change longer to shorter!

20 (lines 380-397) A large part of this section considering large and small bears appears a bit speculative as the authors did not include information concerning body size or body condition in this manuscript. Moreover, I am not fully convinced by the results concerning diet differences

21 (lines 403-430) I find that there is quite a bit of speculation and knowledge is used to try to find a posteriori consistency in contrasting results. In particular, much of the interpretation relies on the abundance of masting vegetation and animal protein, but this information is lacking and the rough estimate of the effect of the proportion of animal protein in the diet is not retained for the use of high quality forage and although retained for selection, the effect appears moderate. I am not sure that the interpretation of the results for the GYE bears is really consistent with the general pattern. Sometimes being big and having a large quantity of animal protein implies better green wave tracking (e.g. GYE, see lines 421-424) and sometimes worse green wave tracking (e.g. Kodiak, see lines 405-408). I have some difficulty in reconciling these groups of sentences (lines 421-424 and 405-408). I may have missed something, but for me there is an inconsistency.

22 (lines 449-453) To be honest, I had been thinking about this explanation since the beginning of the manuscript, because I had in mind that the bear is a large predator and I was a bit surprised that this explanation was not mentioned in the introduction where we consider the bear as an omnivore or even as a "large herbivore". But I probably had the wrong perception of the bear.

23 (Table 1) I think that several of the variables considered in the table could be described here so that the table can be read independently.

24 (Figure 1) n=4 is not a huge sample size for deducing a proportion.

25 (Figure 2) The variations are huge and sometimes not very well distributed (see Fig. 2B), with a link between the mean and the variance. There are 3 points that strongly determine the relationship for Fig. 2B! All axes must have the same scale!

26 (Figure 3) This figure is about variation in the selection of high quality forage, not variation in use. I suggest to explain what A and B are in the legend as in Figure 2. For Figure 3B, there are also 3 points that strongly influence the relationship.

Details
1 (lines 20-21) “may be used to…, which can be used to…”, perhaps you could improve this sentence.
2 (lines 31-32) A bracket is not closed.
3 (line 395) Is the word consumer appropriate here, should it not be conjugated?
4 (line 478) The list of authors is truncated but this is not mentioned!

References
Fortin, D., Hawthorne, L. B., Boyce, M. S., Smith, D. W., Duchesne, T., & Mao, J. S. (2005). Wolves influence elk movements: Behavior shapes a trophic cascade in Yellowstone National Park. Ecology, 86(5), 1320–1330.
Nakagawa, S., & Cuthill, I. C. (2007). Effect size, confidence interval and statistical significance: A practical guide for biologists. Biological Reviews, 82(4), 591–605.
van Smeden, M. (2022). A Very Short List of Common Pitfalls in Research Design, Data Analysis, and Reporting. PRIMER, 5. DOI: 10.22454/PRiMER.2022.511416

Nicolas Morellet

I think the authors have done an excellent job of taking my comments into account. I would have liked to have had some results with and without outliers (in the appendix), to see whether the outliers have too much weight in the results (see figures 2b and 3B), but I leave it to the editor to decide whether these analyses are necessary.

I regret that the authors did not take into account the body weight or body condition of the bears, as I really think they could take into account relative weight (compared with the average body weight of the population). However, this information does not appear to be available.

Best regards,
Nicolas Morellet