Dear Contributors to PCI Ecology,

You have accounted for most comments by the reviewers and myself, but there are some minor issues that need to be addressed.

When you write that you pooled years "in order to maximize the power of our estimation", this is not correct. One uses a statistical model that represents the processes generating the data - if there was a large variability between years, it would be wrong to ignore it, that is pooling the data would lead to a model underestimating the uncertainty (and for example leading to too small P-values or equivalently too narrow confidence intervals). You can argue that based on the data the variability between years is small and therefore the model provides a description of the general pattern, but one does not choose a model in order to get a small P-value. Note also that with respect to estimation, it is precision and/or accuracy which are relevant, power is with regards to hypothesis testing.

The equation of the model (l. 176 of the pdf) is still incorrect I believe. You write y_sd in the model equation and on the next line define y_st (same error with epsilon_sd and epsion_st). And the coefficients of the Fourier series are site specific? If not they would result in the same phenological pattern? Same comment with the variance of epsilon, it is site-specific?

I will wait for your response/changes to decide if I will recommend the manuscript - the suggested changes are relatively minor. If you still disagree with my suggestions, you need to provide a more thorough explanation.

Sincerely yours,

Nigel

Both reviewers provided important comments regarding in particular 1) the original contribution of this paper compared to Wongnak et al. (2022), as the same data are analysed but using a different statistical modelling approach, and 2) the lack of recent references and terminology regarding ticks and disease. Clarifying and revising these points will lead to an interesting contribution on the seasonality of tick behaviour and dynamics.

I will focus on the statistical analysis as I think it is quite central to your analysis. As one reviewer commented, you do not explain why you decided to use log-transformed data rather than the negative binomial as in Wongnak et al. (2022). There is some discussion regarding what is the best approach for analysing count data (see e.g. Ives 2015 for one point of view, and O’Hara et al. 2010 cited in Ives for another). One of the main differences is what the model predicts – the negative binomial model predicts the mean abundance (with a log link function), but the model based on the log-transformed data predicts the mean of the log-transformed value (which is different from the log of the mean values). You are most likely aware of the difference, but you would need then to explain the different modelling choices in the two papers. Moreover, as far as I can understand from your model described l. 169, you assume that the shape of the curve is the same every year (ie there is no effect of the year on the coefficients of the Fourier series – you must have include a site effect on the coefficient to allow site-specific shapes, right? You need to specify this in the equation). This may seem a reasonable approximation judging from Figure 2 (and it is probably what you mean when you mention a “typical “ year), but it is most likely to lead to a large underestimation of the uncertainty in the peak date (which you do not assess in this analyses). I understand that this might not be easy to implement (having different coefficients in different years will I believe result in a non-smooth function), but you should at least acknowledge this limitation of the model used.

In addition, I would also like to point out that the term “mountain” is defined internationally with respect to topography and not climate (you have climate belts such as the montane or alpine belts in some mountains, but this is a different issue, related to vegetation). Snethlage et al (2022) have provided the latest implementation of this international definition of mountains (it is the one developed by the Global Mountain Biodiversity Assessment, and used for example by other international organisations when investigating mountain regions; see eg Thornton et al. 2021, 2022) Clearly some areas defined in Joly’s paper as having a “mountainous” climate are not “mountains” according to the international definition. Please use another term that describe the climate characteristics and does not refer to “mountain”.

You need to provide more details regarding the weather stations used.

Ives, A. R. (2015). For testing the significance of regression coefficients, go ahead and log-transform count data. Methods in Ecology and Evolution, 6(7), 828-835. doi:10.1111/2041-210x.12386

Snethlage, M. A., Geschke, J., Ranipeta, A., Jetz, W., Yoccoz, N. G., Körner, C., . . . Urbach, D. (2022). A hierarchical inventory of the world’s mountains for global comparative mountain science. Scientific Data, 9(1), 149. doi:10.1038/s41597-022-01256-y

Thornton, J. M., Palazzi, E., Pepin, N. C., Cristofanelli, P., & Adler, C. (2021). Toward a definition of Essential Mountain Climate Variables. One Earth, 4(6), 805-827. doi:10.1016/j.oneear.2021.05.005

Thornton, J. M., Pepin, N., Shahgedanova, M., & Adler, C. (2022). Coverage of In Situ Climatological Observations in the World's Mountains. Frontiers in Climate, 4. doi:10.3389/fclim.2022.814181