This paper is very well-written and highly relevant. The assessment of the impact of bias-adjustment techniques on SMILEs is both timely and novel. The authors have clearly put significant effort into considering important steps for bias adjustment. The results section is thorough and addresses all the proposed research questions and even goes beyond them.

I have a few minor remarks:

• In my view, the paper is too long and requires multiple rounds of thorough reading to absorb all the information. I understand it is not easy to cut a paper like this shorter or present it in a simpler way. Nonetheless, I encourage the authors to read the paper again and see whether more plots can be moved to the supplementary section and whether some parts of the result section can be summarized. I think certain plots from the historic analysis can be omitted. Figure 7 is particularly difficult to interpret and I am not entirely sure if I understood its key point. I could have skipped Figure 10 and limited the plots to what is shown for runoff in Figure 11. But even Figure 11 is challenging to grasp, as it represents the final output of multiple subtractions. Again, I understand that it is not too easy to cut this paper short but I think doing the laborious work of summarizing it, helps with readability.
• The authors did not find significant benefits of the multivariate bias adjustment method compared to the univariate approaches, and I find this result reasonable. They attribute this outcome to the well-preserved correlation in this particular SMILE. In my view, the relatively low P–T correlation in the observational data (Figure 4b) also contributed to this result, as there was no strong correlation that needed to be preserved. When the correlation is weak, bias adjustment for separate months may be sufficient to maintain a reasonable dependence between precipitation and temperature. In such cases, I would argue that preserving temporal order might be more important. Ultimately, I would recommend that impact modelers evaluate whether correlation (or even chronology) is important for their specific application and choose a simple method that adjusts just enough, but not more. If the authors agree with this point, I suggest including it in the final discussion and recommendations.
• In section 2.4 (evaluation) does it help to have a table with all the indicators you evaluated, separate for P, T and Q, present and future?

Specific comments:

L3: You can remove this from ‘this internal’ variability.

L136: Mention what the five setups are and then in table 1, in the title mention that the combinations in the last two columns encompasses five bias adjustment setups.

L171: Why not the dependence?

L185-186: The sentence here is somewhat a repetition of L180-182.

L219 and then L253: Why P1 and P2 are introduced in the text but are not used in any part of the result? True that you want to cross validate but if the results are shown all together, is it really necessary to introduce an abbreviation? And then considering what mentioned in the text why Figure 3 is only for one sub period? Why not to show it for the entire historic period? And what is efficiency in this figure?

Does it make sense to already mention in L219 what is later mentioned in L253? And Did I understand correctly that you name the runoff simulation through this joint combination control run? If it is so, please already mention it in the text. I had a bit of difficulty understanding what period Figure 2 is showing.

L233: Change however to instead.  And the whole L233-238 requires some rewriting. The section sounds more like an statement rather than what has been done in the paper.

L249: The term ‘use’ is unclear to me. It is unclear ‘how’ you evaluated it.

L259: the term ‘signal’ is unclear to me. Do you mean the difference between averages?

L265: Remove second. There are two firsts in the previous paragraph. So it is unclear which first this second comes after. I would have personally rephrased the previous paragraph to avoid those firsts.

L271: Remove the time-of-emergence and join the two sentences.

L275: Until here it was not mentioned that you will look at groups of catchment with different elevation levels (or did I miss it?). Cool that you did. But does it make sense to already bring it up earlier in the text and group the catchments in Figure 1 based on the three categories of elevation, to signal this to the reader?

L331-332: Doesn’t this belong to any other section but not the result?

Figure 7: I unfortunately did not understand Figure 7 and its aim after many tries. If it is not only me, please consider both rewriting the section and re-visualizing it, or instead think of removing the plot and the text all together.

L375-376: Somewhat repeats the beginning of the section in L355.

L414: I think setup is better than methods. Not all mentioned in the parenthesis are methods.

Figure 11 is slightly complicated. Instead of showing the subtractions can you show the actual boxplots separately for each of the pairs?

L434-446: This part and Figure 12 is very interesting. However, I think some part of the text belong to discussion. I would have loved to see a plot similar to Figure 9 but for runoff just to see how the methods behave for all runoff simulated components in the catchments.

L514: Unclear what strategies mean here.

L525: Cite the plot for precipitation.

L558: I agree that change preserving is inherently more in line with the aim of future impact studies. But I slightly disagree with the rest of this paragraph: Apart from having the same performance for precipitation, combination of change preserving and individual bias adjustment strategy resulted in very different signal for high flow in Saltina at Brig compared to the rest (Figure 12). One might argue that 99^th percentile is too extreme, but then essentially all methods are more or less similar when it comes to moderate or moderately extreme percentiles. Based on your results, your third point sounds more concrete to me. So my suggestion is to reshuffle third and second point and use an even more cautious tone in suggesting second point.

The paper presents a performance and sensitivity analysis of different climate model bias correction methods and their effect on hydrological simulations of streamflow extremes (low and high flow). By comparing various existing methods across a range of basins in Switzerland, the paper is able to draw useful conclusions about the performance of existing bias correction methods for simulating streamflow in a historical period, and about the sensitivity of future streamflow projections to different bias correction methods.

The methodology is well designed, the paper is clearly structured, and the analysis is comprehensive, with different parts of the analysis logically connecting to one another. My comments are as follows.

1. The abstract should be improved, both in terms of clarity and in terms of better capturing the relevant conclusions of the study. A few pointers:

-line 12: "no clear benefits from using bivariate instead of univariate bias adjustment methods when the SMILE already efficiently simulates the dependence between temperature and precipitation". I wonder how robust/general this conclusion is. Wouldn't independent (univariate) bias correction potentially alter the dependence between variables?

-lines 15 and 16: not clear what is meant by "precipitation and streamflow signal-to-noise ratios" and by "streamflow and precipitation time-of-emergence". This only becomes clear after reading the paper. 

-line 17: "we generally recommend to apply change-preserving and ensemble bias adjustment methods in future hydrological impact studies using SMILEs". To make the abstract more informative, it would be good to clarify in the abstract how this conclusion was reached. The abstract says that there are large differences between bias-correction methods, but does not specify why some methods are preferred over others.

-the abstract could also mention shortcomings identified in existing methods, i.e. which improvements are necessary based on the findings in this study. The need for more research into bias correction methods is mentioned in sections 4.3 and 4.4, but without identifying which improvements are needed, even though the detailed evaluation in this study presumably provided some useful insights on this.

2. The conclusions section (section 5) should be improved: it seems to largely focus on precipitation and temperature rather than streamflow. 

3. The limitations and perspectives section (section 4.4) is currently very short. Several issues identified in the comments here could potentially be addressed in this section.

4. Basin selection (section 2.1): basins with glaciers are excluded from the analysis because the hydrological model does not account for glaciers. It would be good to come back to this in the discussion, i.e. how relevant are the results and conclusions for basins with glaciers, as these regions are especially vulnerable to climate change.

5. One of the conclusions is that differences between bias correction methods are significant. One wonders whether these differences are still significant when considering all other uncertainties in the climate change modeling chain (data errors, model errors, forcing/scenario uncertainties...). Some discussion/reflection on this would be welcome.

6. Model errors: evaluation of the hydrological model against streamflow observations is reported in terms of KGE, which gives an indication of overall model performance (across all flow levels). Since the paper focuses on flow extremes, it would be good to know how the model performs in terms of reproducing the flow quantiles studied in figure 2 and later figures (i.e. the 1%, 50% and 99% annual flow quantiles). For example, this can help put the differences between bias correction methods into perspective.

7. Data errors: "observations" of precipitation and temperature are based on gridded (interpolated) meteorological station data, which are used as benchmark ('ground-truth') in this paper (line 155). To what extent does bias and noise in these data affect the results? E.g. typical sources of bias are under-catch of precipitation gauge measurements (especially for snow) and the absence of stations at high elevations.

8. Evaluation: for evaluation of the bias correction methods, the authors adopt a method presented by Suarez-Gutierez et al. 2021; specifically they quantify the fraction of observations that fall in the 75% ensemble confidence interval. Note that those same authors also look at other aspects, e.g. they suggest making a rank histogram which should look uniform (see their figure 1). A cdf version of the same idea is in Laio et al. 2007 (figure 2 in https://hess.copernicus.org/articles/11/1267/2007/). It seems this would allow for a more complete evaluation of the ensembles. Can the authors comment on whether these methods are applicable here and why they were not considered?

9. Consistency in terminology: on line 136, we are introduced to "five bias adjustment setups". Later on, a distinction is made between 3 bias adjustment methods and 2 ensemble adjustment methods (e.g. figure 12), while figure 10 refers to these combinations as bias adjustment options. Would be good to be consistent and for example introduce the naming used in figure 10 from the start and use it consistently throughout the paper.

10. Line 185: "We run the adjustments at the grid scale rather than the catchment scale to avoid adding a downscaling step to the procedure, and because the catchments are of different sizes." The reasoning here is not clear to me, i.e. how does bias adjustment at the catchment scale add a downscaling step (compared to adjustment at grid scale followed by moving to catchment scale), and how does catchment size come into play?

11. Overall structure of the results section: even though this section already flows quite nicely, you could consider splitting up section 3.2 into two further sub-sections (precip/temp and streamflow), and using the same split in section 3.1 (precip/temp and streamflow). Currently, section 3.1 starts with streamflow, so opposite order of section 3.2. Not super crucial, but readability may improve by breaking up the results into smaller pieces and using consistent order in sections 3.1 and 3.2.

12. Figure 2: clarify what is meant by "control runs" - I know it is mentioned in the methodology section, but it should be clear from the figure caption. Also, the figure axis should make clear which variable we're looking at. Suggest to rename bias adjustment method "raw" to "none" or "unadjusted". And I assume these are box plots, would be good to explicitly mention that. And which variability is captured by these box plots? Is it variability across the 87 basins?

13. Figure 2 and other figures focus on the 75% ensemble interval for streamflow. Why did you pick 75% and would your conclusions change if you pick another percentage? See also comment 8.

14. Why does figure 3 show results for one of the evaluation periods whereas figure 2 shows results for both? Also, the color bar title ("fraction of control runs") should make clear that we're looking at streamflow.

15. Figure 10: figure/axis title should make clear we're looking at precipitation. Same for figures 11 and 12, make sure the figure/axis title mentions 'streamflow'.

16. Figure 12: noise is expressed as %. Is this the coefficient of variation? The axis title calls it standard deviation?

17. Line 587: "ensemble adjustments combined with the change-preserving method are less efficient for the tails of the precipitation and temperature distributions in the historical period, probably because the raw change signals are small compared to the internal variability for many catchments". This is not clear. How does the climate change signal (second part of sentence) affect performance of the bias correction method in the historical period (first part of sentence)?

18. Line 128: biased --> bias