Dear authors,

Thank you for providing some responses to the referees’ comments.

You will find below some comments on the above as well as some additional comments. Both referees found this study quite valuable as I do. However, in general, I find that some interesting referee comments called for either much deeper responses that you provided, or simply actual responses to some parts of the comments. I will highlight them below, and I would really appreciate motivated and extended responses, that would then be transferred into the revised manuscript.

On responses to referee #1
- I would agree with referee #1 that even if I have no doubt about the novelty of this study, it should be clearly demonstrated in the introduction through a thorough comparison of literature review (including the references suggested by the referees).
- The comment on the use of single hydrological model would in opinion call for some insights from the authors. Indeed, a calibration is highly dependent on the model structure, and some conclusions even from the reference period may not hold with a different model. This has also been pointed out by referee #2. I would therefore appreciate some more comment on that in the revised manuscript.
- The first part of the comment on the uncertainty analysis asks a specific question on the effect of different sample sizes on the robustness of the chosen dispersion indicator, which has not been responded. This question also holds for any anova method, so I would appreciate some comments on that.
- “delta change approach”: I believe there is here some confusion on these terms between the referee and the authors. As mentioned by the referee, the delta change approach refers to a method of obtaining future climate forcings for impact studies, which consists in (1) computing climatological differences between a future time slice and a present-day time slice of a given projection (initially from a GCM run, possibly downscaled), and (2) applying such “deltas” to observed climate time series. This is different from analysing impact changes given such forcings, changes which are commonly examined with reference to values simulated during the present-day period, independently of the method used for obtaining future climate forcings. This confusion is also present in the manuscript: no clear distinction is for example made between the two steps, as noted by referee #2 (comment starting with “2.1 low flow projections”). I would therefore strongly encourage the authors to try and remove any possible confusion, to adopt widely accepted expressions, and possibly restructure the data and methods sections.
Moreover, there are important details missing in the way such “deltas” are applied to observed time series. The main question is: how are monthly precipitation changes applied to observed daily time series? Are all positive values scaled? Is the number of rainy days increased? Any hybrid solution? The delta change method originates from times (a decade ago) when downscaled projections were scarce and transient GCM projections rarely available. As mentioned by both referees, studies have since shown that this approach is not entirely satisfying, mainly because it does not take account of changes in interannual variability (which has recently been pointed out as the main source of uncertainty in near-term projections for global variables, up to mid-term or even long-term projections for more local hydrological variables), and because choices like the one mentioned before have non-negligible consequences on hydrological impacts. It is especially the case for summer low flows that are quite sensitive to rainfall occurrence. In conclusion, this would require some serious discussion, and more than a rephrasing.
- Referee #1 asked about the nature of a point located outside of Austria in all maps, and this did not prompt any response from your side. Please do comment.
- The comment of referee #1 on the possible difference in Q95 values in Figure 5 makes me wonder how Q95 values are actually computed (I believe independently for each period present/future). This is not clearly stated in the manuscript, please confirm.

On responses to referee #2

- On the definition of uncertainty: I agree with referee #2 that the manuscript is somewhat confusing on this point. Once again (after my initial comments to the authors on the initial version of the manuscript), I urge the authors to use widely accepted expressions.
- I appreciate the efforts of the authors to engage in a more formal analysis of variance following the recommendations of referee #2.
- On the choice of climate projections: in addition to the referee’s comments, I would add that some discussion is required on the unbalanced sample of projections with respect to the emissions scenarios, even if only to state that their effect is nearly equivalent for such close time horizons.
- Delta change approach: again, the response made to this comment is in my opinion unconvincing and too cosmetic (see my discussion above).
- Discharge unit: the sentence is actually confusing, because it includes “precipitation”. Additionally and anecdotally, the lower bound of specific discharge cannot be technically zero if we believe your statement that no zero value was found when computing MlogE.
- GHG scenarios: you do not happen to have responded to the first part of the comment on the relevance to describe GHG scenarios. See also my comment above.
- P12405L8: I believe the confusion may arise here for improper uses of comparatives (as noted by referee #2), as in many other places in the manuscript.
- P12405L11: Here again, this referee comment is in my opinion quite relevant and at least calls for some discussion on a potential artefact when comparing ME and MlogE. Please provide some comments.
- P12408L21: Again I feel that some confusion arises from the intermittent use of “low flow” throughout the manuscript to actually mean “Q95”. I therefore again encourage the authors to be more rigorous with the terms used throughout the manuscript.
- P12409L1: This is again a quite light response to a yet quite interesting comment. Please provide some more depth to your response.
- P12411L8-10: Again, I can’t see in your text any response on the first part of the comment relative to the use of a single hydrological model and the generalization of the results. Please provide some actual comments and relevant changes to the manuscript.
- P12412L2: I am afraid I don’t understand the proposed revised sentence.

Additional comments

- Figure 1: As only 2 classes of catchments are considered throughout the manuscript, this figure should rather identify these instead of continuous (and not quite adapted: early January and March have much more similar colours than November and January) seasonality strength.

As a conclusion, I believe the manuscript has solid scientific contents and brings novelty to the field. I therefore recommend the authors to take account of all referee comments as well as my own ones to revise the manuscript.

Best regards.

Dear authors,

Referee #2 has provided a further review and found the manuscript substantially improved. I fully agree with this conclusion and I would like to thank you for your efforts on revising the manuscript.

I can now accept the manuscript for publication in HESS, provided that you address the technical corrections suggested by Referee #2 as well as my own ones listed below:

- I found several typos/mistakes in the manuscript (on top of the ones spotted by Referee #2), plus some trimmed (and unclear) expressions like “summer and winter dominated basins”. Please have a careful read of the manuscript.
- P2L1: the figure “60%” is not understandable as is in the abstract (60% of what?). Idem for L9 and L10. It has to be clear that these figures denotes a spread in relative changes, expressed in percents (this is not straightforward from the abstract alone, which should be self-contained).
- P1L15: I would add “respectively”.
- P1L15-17: I doubt this sentence is consistent with the actual findings reported...
- P6L5: I believe you meant “low flows” instead of “floods”.
- P7L25: “seasonally at the regional scale”. Please rephrase: I believe you meant “for two low flow regimes and for individual stations over Austria”.
- P8L18: I would be much more comfortable in reading “variance” instead of “variability” here.
- P9, equation 17: It has to be made explicit that similar equations may be written for factors B and C.
- P14L30-31: There are also counterexamples of high Q95 variability in this large-SI cluster. Please rephrase.
- P16L27 and Figure 14: Aridity should be defined somewhere in the manuscript.
- P18L24 and following. As for the limitation of this study due to the use of a single hydrological model structure, it should be mentioned in the manuscript that only one RCM is considered here (and both ENSEMBLES and CORDEX studies found that RCM uncertainty is far from being negligible for hydrology-related variables).

Best regards.