|This is my second review of the paper entitled "A gridded multi-site precipitation generator for complex terrain: An evaluation in the Austrian Alps" by Hetal Dabhi and co-authors. My general opinion about the paper did not evolve much since my first review because, except for the implementation of a cross-validation experiment, most of my comments have been rejected without convincing counter-arguments.|
To start with a positive note, I am glad to see the addition of a cross-validation experiment, which is convincing.
A more debatable aspect is the new statement (L 151) that "elevation dependence in the covariance structure is the natural assumption in complex terrain". I may accept "is a natural assumption" if more details were given (for instance by discussing in more details the references Wilks (1999, 2009)), but it is definitely not "the" natural assumption.
Beyond the choice of phrasing, I red with interest the two above references that are cited by the authors to justify the choice of an elevation dependent covariance. I acknowledge that in Wilks (1999) an altitude dependent covariance function is used, but I would like to draw your attention to the fact that in this study, the authors used a model selection step which leads to sometimes remove altitude from the covariance function of precipitation occurrence (2 months over 12), and most of the time for precipitation amounts (7 months over 12). In my opinion this shows that this kind of parametrization is fair (and I would like to emphasize here that I have no problem if you want to keep it), but should be handled with care (hence the necessity to discuss it thoroughly, and not take it as obvious). In addition, it should be noticed that in Wilks (2009), the same author does not use altitude in the covariance function of precipitation anymore, but keeps this parametrization for temperature only. Which makes sense to me, because vertical lapse rates are more obvious for temperature than for precipitation.
To sum up my opinion on this point: I am ready to be convinced that the proposed covariance function incorporating altitude is worth implementing in your context, but you need to put a bit more efforts in justifying why.
Finally, there are several aspects that I still find problematic:
1) I have the impression that the absence of nugget in the Kriging step may generate artifacts, and your response to my comment as well as the associated changes in the manuscript (which are restricted to acknowledge the absence of nugget) are not convincing.
Kleiber et al. (2012), which was the starting point for the present study, used a nugget effect when kriging model parameters. You decided to remove this nugget. This may be Ok (I honestly don't know), but you have to justify it. This can be done either by explaining why do you think there is no small scale variability in the parameters to interpolate, or (even better) by showing that these parameters do not display small scale variability. For the later option, the best solution is probably to show that the empirical variograms of the parameters interpolated by Kriging are close to zero for short lags.
2) The figure R1 displaying scale paramater=f(elevation) and shape parameter=f(elevation) in the response to my major comment 2 (in the response to reviewers file) does not show any clear relation between the parameters to interpolate and the external drift, and therefore does not really justify KED.
In the same line, I don't think that the new figures 16 and 17 (formerly Fig 19 & 20) show a clear advantage of KED vs OK, nor of isotropic vs anisotropic covariances. This is in line with the comment 14) of Reviewer#3: "Maybe there are some improvements, but I don’t have the feeling that they are ‘considerable’!", and the changes made in the manuscript (L 567) are in my opinion too minor to reflect this shared concern.
I therefore strongly recommend to the authors to rewrite the discussion of Fig 16 and 17 to clearly acknowledge that the improvements associated with the use of KED and anisotropic covariance are rather limited.
3) The explanation about the absence of outliers at Prutz station (in the response to reviewers file) and the reason why you don't want to investigate it further are not convincing (that is the least I can say).
Why don't you want to display the data to understand what is going on?
Either the data from this station is an outlier, and removing it will improve the performance of your model. Or there is a micro-climate at this location, and this is interesting to point out. In any case this must be discussed in more details.
4) Your response to my minor comment 10) (i.e. why using only NAOI as covariate linked to atmospheric circulation) is not satisfactory.
5) Your response to my minor comment 2) is not satisfactory. Most of your covariates for Xo(s,t) are functions of t only (hence constant through space) (e.g., cos(2*pi*t/n), sin(2*pi*t/n), etc.). What I propose is to add a covariate that is function of s only (hence constant through time). Xo(s,t) is indexed in both space and time. I hope that put this way you can see the symmetry of the problem in space and time, and then the possibility of using altitude as a covariate.