Final response Floriancic

Dear Marius and co-authors,

Thanks for your online-replies to the reviews. The manuscript has received differing reviews, recommending minor revision, two times major revision and one rejection. Based on the details of the reviews, I invite you to submit a substantially revised version of the manuscript for further consideration. The revised manuscript will then be reviewed again by at least two reviewers in order to decide further.

My editorial assessment based on the reviews in particular identified the following necessary major revisions:

1) Working out the sufficiently original contribution: Three reviews contain the phrase 'not surprising' when describing the results of the study. That itself does not hinder publication, but the added value of the findings has not been sufficiently worked out yet. R4 finds the hypotheses too weak, an assessment that is also reflected in R2 and illustrated by the summary written by Ryan Teuling's students. R2, R3 and R4 find the 'initial analysis' on seasonality particularly redundant with previous work, confusing, or at least not original enough to warrant the space it takes in the manuscript. This suggests that the necessary conclusion to continue with summer low flow may also have been based on a thorough review of existing work on low flow seasonality. In what way does the study go beyond previous work, e.g. the maps in HADES, the regime stability classification for the "Modulstufenkonzept" and all the underlying research?
The reviewers do make some general suggestions, where to look for the added value, for example that "results [of merely measuring whether there is correlation] could benefit from an actual quantification of the relative contributions" or to "better use the added value of the large dataset to explain controls" or really take up the 'shaping' idea from the research questions. Please take the combination of these reviewer comments seriously into account in the revisions to prove progress by and original contribution of the study.

2) The reviews also raised concerns about terminology, in particular the use of 'extreme'. I agree that this terminology requires a specification, what frequency this refers to and that 'low flow' and 'streamflow drought' need to be distinguished. Regarding terminology issues pointed out by the reviewers, please make sure your terminology meets international conventions or clearly explain and reference any Swiss terminology used. For example consider the WMO Manual on low flow estimation (Gustard and Demuth 2005) or the textbook on low flow and drought estimation methods by Tallaksen and van Lanen (2004) . Also I suggest to draw parallels to recent research on drought propagation that correlated SPI and SPEI (essentially not much different from your non-standardized precip accumulations) as well as studies using basin properties/catchment characteristics for regionalization in general.

3) Two reviewers (and I) also I find the mixed results and discussion confusing as it is not easy to distinguish plain results against wider interpretation with relation to other studies and current debate. The reviewers and I will review this very carefully again and I would highly recommend changing to a clear separation of the two as part of the revisions. It may in fact help demonstrate the added value of the analysis (see comment 1).

4) Subjective choices made, incl. the >3 sd exclusion, widow sizes for P accumulation, or the 1200 m.a.s.l., are not acceptable without good argument by physical reason or empirical proof. I expect the revised manuscript will either provide sound reasons for these decisions or test the results' sensitivities.

5) I take the liberty to add one missing consideration that has not been picked up, but that I find crucial to be addressed for the credibility of the study: magnitude and seasonality of observed low flows can be altered by water management operations, river regulation, sewage treatment plant return flows, the filling of reservoirs and minimum flow release from them, hydropeaking etc...(e.g. Pfaundler and Wüthrich, 2006). All these issues are very prominent in Switzerland and metadata on e.g. minimum flow releases and water transfers is available and can and should be used in any analysis. At the moment, the study considers only natural climatic causes of low flows. It also does not consider the effect of trends and jumps due to human interventions over the study period. The minimum work to do is to carefully test for those, remove any records that show signs of human impact and carefully discuss how common water use and regulations may affect (intensify? compensate?) the identified climate-low flow relations.


Technical editorial comments

For the revision, please consult the manuscript preparation instructions - symbols and mathematical notation and avoid multi-letter variable names, in particular see suggestion of not using "ET" (or here "PET") in the HESS instructions.

Please mitigate some of the excessive citations (parentheses with eight references are not useful). Ideally be more specific about the relevance of the individual references to this study.

Please note that manuscripts "in review" cannot be cited and will have to be removed from the references.

Figure captions: As also noted by reviewers, add legends to figures rather than writing long descriptive caption texts and in particular shorten the captions by removing duplicate legend/caption text and long explanations.

First letter of axes labels should be capitalized.

Regarding R1's comment on the data statement and your reply: that's fine - please make sure that a list of station IDs and the address/who to contact for each station ID is included with the published dataset and/or as supplement.


References

Gustard A., Demuth S. 2008: Manual on Low-flow Estimation and Prediction. Operational Hydrology Report No. 50. WMO-No. 1029. Geneva.

Pfaundler M., Wüthrich T. 2006: Die Saisonalität hydrologischer Extreme. Das zeitliche Auftreten von Hoch- und Niedrigwasser in der Schweiz. Wasser Energie Luft 98: 77–82.

Tallaksen L.M., van Lanen H.A.J. 2004: Hydrological Drought: Processes and Estimation Methods for Streamflow and Groundwater. Developments in Water Science 48. Elsevier, Amsterdam / Oxford.


Best regards,

Kerstin

Dear Marius et al.,

thanks for resubmitting this revised version of the manuscript. In general the two reviewers that assessed this new version found that many of the critical aspects addressed. However, some concerns remain and one reviewer has requested further revisions that require reconsideration before a publication decision is made. Hence I would like to invite you to resubmit a revised version for reconsideration.

In summary, both reviewers still raise concerns particularly about
a) lacking clarity of the data selection and analysis of sub-samples (streamflow records used and seasonal windows analysed) and
b) about choice and terminology of the metrics analysed, questioning in particular the choices made to analyse an impact of SWE.

I re-read the Methods Section 2.3 to assess these concerns and also did not find it sufficiently clear. Unless the methodology is properly written out stating for each analysis: the data sampling, the variable used, a hypothesis for the test applied and the assumptions on the data this test requires, and for statistical models ideally also the equation, I see no possibility to accept the manuscript for publication.
For illustration perhaps, I try to explain my sources of confusion while reading section 2.3: after the at-site time series correlations are stated as a method, line 156 then suddenly introduces a "sign test for the distribution of the individual rs values". So there is a switch from at-site to a regional test? But what is the (regional/spatial?) hypothesis tested here, which test exactly is used? Then, the text jumps back to at-site correlations, then again to a regional sub-selection, which is suddenly introduced (another one?)... Then the GLM? Is this a regional model again or a number of at-site models (predict Qmin spatially or temporally)? How exactly is this 'fraction of the R2' determined - as far as I know there are many different methods to do this, again making certain assumptions. Finally, I can understand what has been done only by looking at the results and that is not sufficient. Some analysis (like the human influenced catchments) are even not at all introduced in the Methods section. All (!) sampling choices and analyses carried out need to be clearly understandable from reading the methods section alone. I think this revision is easy to implement.

Please also thoroughly consider the concerns of R2 regarding climate anomaly vs absolute low flow. Line 60 of the ms states: " The annual lowest flow is (for a particular year) an exceptional flow condition, so we expect low flows to occur after weather conditions that are atypical (for that same year)." This sentence is very hard to read, but as I understand it, the assumption is that any annual minmum flow must be caused by seasonal climate anomaly. For very stable glacial and nival regimes, the Qmin of which is almost in the same week-month, I doubt this is correct. Please check if the statement is generally applicable like this and make it more clear.

I think we don't doubt the result of the SWE impact, but it will only be credible if the assumptions are well justified. I agree with the R's concerns that the reduction to using 1 March snowpack as an indicator may be a lost chance and certainly will require better argument for this choice. The rest of the mountain-world uses April 1st snowpack for water resources planning! I strongly suggest that you add some proof (could be literature) that for Switzerland March 1st is the 'consensus' peak-of-snow-accumulation and really reflects the 'end-of-winter' storage of snowpack+groundwater well in CH.

A concern not yet sufficiently well responded to is the one-sided outlier removal. The 'three-sigma rule' intends to detect statistical outliers: on both ends of the distribution. Removing them from analysis is another step that needs argument. The underlying assumption of the statistical view is that such values are unlikely/physically impossible and must be wrong due to the measuring technique. Eliminating subjectively the outlies in (only) one tail of the distribution because (?) they are inconvenient (?) represents a non-acceptable data selection. The lowest flows will likely also be not well-gauged! I cannot accept the simple addition of a reference to the general three sigma rule paper as a response to this concern. I also don't understand why the removal would be useful. Having higher flow values and hence more variability in the sample that is correlated with preceding climate anomaly (which will for sure be not a deficit when there is high flow - unless it's caused by snowmelt and then that is relevant!) should only be beneficial to finding a higher correlation. If for some reason high flow values are not wanted, another sampling strategy up front is necessary (like annual series vs partial duration series in flood stats - "peak over threshold", for low flows there is a reason why normally events under threshold are commonly used in low flow statistics).


Additional editorial comments:

I am afraid the abstract could better reflect the work - maybe a result of the revisions?. It has redundancy and contradictory statements in several sentences. The repeated focus on the comparison to larger scale Europe does not match title nor the real contribution that this study now makes. I suggest to revise it to bring out the contribution better and attract the right attention.

Yes, I will insist in changing PET to the likewise common Ep for example if it is used as a variable name. If it's only used in text and as acronym, please do as you like. In any case, just because others have done it wrong is not a reason to do it wrong also.

Regarding figure legends and captions: HESS house style asks for "concise figure captions". There are different styles for figure captions, yes, and that can be accommodated. However, in the current version of the manuscript the same information on figures is sometimes repeated 3-4 times: in a header over the figure (really unnecessary!) and exact same text in the caption text under a) and b) for example, then in the following explanatory sentence again, and in the text of the manuscript. Please revise this for conciseness - in particular do not repeat colors if there are legends. Repetition does not make anything more clear but is instead confusing for readers.

Dear Marius et al.,

thanks for revising the manuscript once more.
I now consider it ready for publication. Ref 2 noticed a few typos etc. and a few inconsistencies in the text that you should check and might consider as part of your final manuscript preparation before file upload.

Thanks and best regards,
Kerstin