Summary:

This paper presents a comprehensive analysis of the use of the Kling-Gupta Efficiency to configure conceptual models for accurate simulation of droughts, floods, and the transitions from droughts to floods. The authors use 63 basins, 4 conceptual models, 5 different KGE formulations, 3 streamflow transformations (Q, 1/Q, average of both), and 4 different weights for each KGEs' variability component. They investigate (1) the performance of the models for extreme events detection with the Critical Success Index (CSI); (2) the simulation of various hydrologic states and fluxes (streamflow, evapotranspiration, snow water equivalent, soil moisture, baseflow) with the Nash-Sutcliffe Efficiency; (3) the correlation between catchment attributes and CSI values; (4) the relative importance of different parameter values; as well as (5) the relative importance of all tested factors in terms of CSI through with an ANOVA approach. Conclusions suggest (1) that higher KGE scores for streamflow simulation do not necessarily imply good performance on other variables (such as ET or SWE) or other metrics (such as CSI and NSE); and (2) that model structure, catchment attributes and forcing data quality are key controls on our ability to accurately simulate extreme events.

Assessment:

Dear authors,

I have completed my review of your paper. It is comprehensive and interesting (as well as ambitious), but I believe further work is needed before this manuscript can be published. I will upload a PDF with individual comments, and attempt to summarize what I consider most important here.

[1] First, let me say that I recognize the sheer amount of work being presented here. However, this can be as much a weakness as a strength. Right now my feeling is that this manuscript is trying to do too much at once. The analysis is very complex, the details don't always get the attention that I think they need (I tried to highlight these instances in the PDF), and part of the methodology seems only explained in the Results sections. You are asking quite a lot of the reader throughout, and I wonder if a more streamlined and focused manuscript wouldn't present a clearer, more easily digestible message. In the end it is of course the authors' choice what to present but I wanted to point out that I found the manuscript quite difficult to follow at times due to the sheer complexity of the work being presented.

[2] Second, I think there are some technical questions/concerns that should be addressed.

[2a] Primarily, I think there are reasons to believe that some of the conclusions about the importance of model structure may be artifacts of improper calibration of the GR5J and GR6J models. It is my understanding that GR5J is so close to GR4J in terms of structure that it can actually become GR4J if its X5 parameter is set to 0. The GR6J case is less clear to me, but looking at the model schematics side-by-side, it should be rather close to GR4J in terms of capabilities. However, Figure 4 shows very large differences in the calibration KGE scores between GR4J on the one hand (these are higher), and GR5J and GR6J on the other (these scores are much lower). This suggests that something has not gone quite right during the calibration of GR5J and GR6J: if GR4J is strictly a subset of GR5J, than the calibration should be able to find those parameter sets that make GR5J (that currently has the much lower scores) mimic GR4J (which currently has the much higher scores). A similar argument could (should?) apply to GR6J. My first guess would be that the ranges for parameters X5 and X6 were too restrictive, but I could not find the parameter ranges that were used for calibration in the document and thus cannot confirm this. To me, this aspect of the study needs considerable attention because it affects all the analysis that comes after.

[2b] I'm not fully convinced of the value of adding precipitation and temperature correction factors to the calibration procedure. I think there is a real risk that this makes the calibration problem (even more) poorly constrained by increasing equifinality during parameter selection, and the benefits of adding these parameters are unclear to me. These two parameters are mainly used to support the conclusion that more accurate forcing data is helpful, but I think this is obvious. The drawback of adding these parameters (letting the calibrating procedure compensate for other shortcomings in the modelling chain by adjusting the model inputs; i.e. getting the right results for the wrong reasons) are insufficiently discussed in the manuscript.

[2c] As far as I can tell, many (all?) of the comparisons between different setups are based on visual assessment of the figures shown in the manuscript. I believe the use of statistical tests would be more appropriate to quantify the extent to which decision X leads to different modeling outcomes than decision Y.

[3] Finally, I think some of the statements made in the paper are too general. In particular, the first conclusion presented in Section 6 is: "Drought events are better captured by hydrological models than flood events." This is, in my opinion, too bold of a claim for the results shown in this work and needs some sort of mention about the study constraints this conclusion is valid within (number of models, types, number of basins, locations, etc.). I believe this applies to a few other statements in the paper and tried to highlight these in the PDF.

I hope these comments are helpful in some way. 

Kind regards,

Wouter Knoben