Dear authors,

The reviewers have confirmed the potential value of your manuscript to the readership of HESS, but they also identified a range of shortcomings and open questions. I would like to thank the reviewers for their critical reviews and particularly for taking the time to suggest specific improvements. I hope that this process will result in a valuable paper and a satisfactory result for all.

Thanks also to you for your insightful responses to the reviewer comments. Based on the very detailed and constructive reviews and your responses, I would like to encourage you to submit a revised manuscript, and in addition to the changes you already announced, pay attention to the points I listed below. When submitting a revised version, I would appreciate if you could respond point by point and indicate what changes have been made in the manuscript. Ideally, you could also attach a manuscript with changes highlighted, which would likely expediate subsequent review. If you prepared your manuscript in latex, such a document can easily be generated using the program latexdiff. Could you also use continuous line numbering instead of re-starting at the top of each page? This might avoid some confusion about line numbers, which I experienced when reading the reviews, and make the review a bit easier. Thank you.

Given some of the strong but also constructive comments made by the reviewers, I plan to give the reviewers another opportunity to comment on your revised manuscript. Some of the reviewers' comments suggest that the study may only have a regional relevance. In response, you pointed out that papers of only regional relevance have been published in HESS before. In my eyes, setting minimum quality standards based on papers published previously is out of question, as this would inevidently lead to degradation in the quality of the journal (any low quality paper escaping scrutiny would be used as a new low limit). In fact, I believe that each paper has to demonstrate a clear increase in quality and information gain compared to previous publications. Therefore, I wish to urge the authors to take any measure that increases the paper's relevance to the readership of HESS. What are the new insights we gain, how will the paper advance science? I tried to add some more suggestions below that might be helpful in this respect. In this context, I did not find a link to the data set you generated. Please describe how the data can actually be accessed. Otherwise, your analysis is not reproducible and the data product not useful for the readers.

Best regards,
Stan Schymanski


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List of requests/comments

1 - Objectives of the paper: Although Reviewer #3 is the only one that pointed out the lack of clear objectives, I agree that this is indeed missing. This does not necessarily require re-structuring of the whole paper, but formulating the specific objectives of the paper in a condensed and informative form. It could easily be done in the last paragraph of the introduction, using dot points or a list, as suggested by the reviewer. You could then return to these objectives in the conclusions.
In doing so, please consider the reviewer's concern about the limitation of the study to the UK only. There is some discussion putting the results in a broader context, which is good, but it may be helpful to discuss similar work that has been done for other parts of the world and how the present study extends or improves on previous attempts.

2 - Uncertainty in data: Please discuss in the revised manuscript uncertainty in the data as requested by Reviewer #1 and please reconsider the suggestion by Reviewer #3 (the reviewer's Point 4) to plot trends obtained from station data in comparison to trends obtained from the gridded data. If station data of pan evaporation is available for sufficient stations, Suggestion 5 made by reviewer #3 could also be considered to assess reliability of the data and methods.

3 - PET, PETI, AED: As pointed out by Reviewer #1, the discussion of PETI is very confusing, and your response seems to reveal more confusion. The evapotranspiration from wet leaves, in my understanding, can hardly be lower than transpiration by dry leaves. When the leaf surface is wet, it is irrelevant for ET what happens to stomata, as ET is dominated by evaporation of the liquid water film on the leaf surface. Your discussion about suppression of transpiration in favour of evaporation may be misleading, as it suggests that you are actually able to distinguish between actual transpiration and ET. Please remove this part of the text and clarify that the addition to PETI (compared to PET) represents evaporation from wet leaf surfaces and is therefore not limited by stomata, unless I misunderstood something here. Or, even better, use the Penman equation and remove interception altogether, as suggested below. Please also check the text carefully to avoid any other suggestions that may mislead the reader to believe that PET represents actual transpiration, in favour of clarifying that it is a climatic variable, where stomatal resistance is merely used as an invariant reference. A clearer discussion of your definition of PET in the context of other definitions commonly used in the literature may also alleviate the major concern expressed by Reviewer #3, that reference crop ET is not commonly used to define PET. I agree with you that there is nothing wrong about using expressions that do not have a unique definition in the literature, as long as they are clearly defined in the present paper. However, your discussion of PETI suggests to me that confusion remains and I would like to urge you to take any measure to improve clarity and avoid confusion. On this note, I do not agree with Reviewer #3 that you should consider soil moisture effects on stomatal resistance in this study, as you are indeed referring to a measure of *atmospheric* evaporative demand. Please consider adding references to "atmopsheric" whenever appropriate, including in the title and abstract, as suggested by Reviewer #3, to avoid confusion with e.g. "canopy atmospheric demand", which might be what motivated some of the comments made by Reviewer #3. Perhaps the reviewer's suggestion to drop the use of the PM equation in favour of the Penman equation could also help avoid some of the confusion, as it does not require mention of stomatal resistance and is essentially the PM equation with zero stomatal resistance. I am not sure what you mean by "wind-humidity deficit demand", allegedly not included in the Penman equation. Penman's wind function includes the wind effect and humidity is explicitly included in the equation, so what is your point here? Furthermore, use of the Penman equation instead of the PM equation with some prescribed stomatal conductance would render the explicit consideration of interception obsolete, and avoid one of the problems mentioned above and the difficulties in estimating interception, as pointed out by Reviewer #3 in Comment 22.

The above discussion actually made me realise that it might be very interesting to look at the trends in PM-ET at two different values of stomatal resistance, e.g. 0 s/m (i.e. equivalent to the Penman equation) and 1000 s/m (equivalent to water-stressed conditions), which are likely to be quite different, as the sensitivity of transpiration to wind speed at high stomatal resistance is opposite to that at low stomatal resistance (Monteith, 1965; Schymanski and Or 2015). These differences could give us a better appreciation for the meaning of the trends in atmospheric forcing for real leaves, and generate insights that previous studies were not able to generate.

4 - Reviewer #2 is right that your computation of trends on p15 li10-11 may propagate a wide-spread mis-conception that the mean of a product equals the product of means. Even if relaxing this assumption does not change the results very strongly, as you describe in your response, the reader would benefit from being pointed to this problem and informed that in this case, the choice of procedure did not have a significant impact on the results.

5 - Tables 2 and 3: Reviewer #2 asked to replace the contributions to trends in PET by actual trends in Table 3. Another possibility would be to extend Table 2 to be more consistent with Table 3, i.e. instead of providing trends for the whole continent, provide trends for each region, and then leave Table 3 as it is.

6 - Fig. 11: Reviewer #2 made some points about Fig. 11 that you did not respond to. I actually struggled to understand the meaning of Fig. 11, as it is not sufficiently described in the results section. Only when reading the comments by Reviewer #2, I realised that the first symbol in each panel represents the overall annual trend taken from Fig. 10, while the first bar represents the sum of all following bars. If this is the case, I agree with the reviewer that there seems to be a problem in the numerics, as the sum of the contributions of each component should recover the total overall trend. Particularly in the aerodynamic components, the sum of the contributions falls short by order(s) of magnitude in recovering the total trend. Please explain or correct the analysis.

7 - Trend maps: Even if the production of trend maps may be perceived as suggesting over-confidence in the results, I strongly agree with Reviewer #2 that it would be useful for the reader to see what data the regional averages are based on. For example, the reader may ask herself if some unexpected trends could have resulted from outliers in the spatial data. Therefore I would suggest to present such maps in the appendix, where it is less likely to suggest over-confidence in data quality.

8 - Air pressure: Could you please check that neglect of variations in air pressure has negligible effect on the results in the highlands, in addition to the lowland check you already performed. Reviewer #2 specifically pointed to potential bias at higher elevations, so it is important to exclude or at least quantify such bias. Please also mention the points made by Reviewers #2 and 3 in the text to make the reader aware of the potential shortcomings.

9 - CRU vs. MORECS: please clarify which data stream was taken from which source, as requested by Reviewer #2.

10 - Vapour pressure lapse rate: This was a very insightful discussion between you and Reviewers #2 and 3, which I think that the reader would benefit from. Could you include a paragraph in the text reflecting the main points?

11 - DTR: Reviewer #2 made the valid point that the relevance of the daily temperature range (DTR) in the present paper is not adequately discussed. Could you please include such discussion? I believe that this could be a very insightful addition. Also, in your response to Comment 16 by Reviewer #3, you state that MORECS only provides daily mean air temperature. Could you explain how you obtained DTR, then?

12 - Fig. 4: Considering the comment by Reviewer #2 and your response, I suggest to add a panel to Fig. 4 with relative differences, as any discussion in the text has to be easily verifiable by looking at the presented data.


REFERENCES
Monteith, J.L. (1965): Evaporation and environment. Symposia of the Society for Experimental Biology 19, p.205–234.
Schymanski, S.J. and Or, D. (2015): Wind effects on leaf transpiration challenge the concept of “potential evaporation.” Proceedings of the International Association of Hydrological Sciences 371, p.99–107. doi: 10.5194/piahs-371-99-2015.

Dear authors,

Thank you for your thorough revision of the manuscript. The reviewers confirmed that the manuscript is worth publishing in HESS, subject to addressing a few additional points. Referee #2 made an excellent point about looking at absolute vs. relative humidity driving changes in AED. Since the ideas presented in this referee report go beyond the usual reviewer contributions, I asked for permission to disclose the referee's identity to you, in case you wish to include the idea in the present paper and acknowledge the reviewer's contribution or offer co-authorship in a follow-up paper. If this is the case, please let me know and I will send you the contact details separately.

I leave it up to you how far you want to follow up on the above idea in the present paper, but I would expect that you at least raise the reader's awareness of the point made by the reviewer and perhaps present some results about trends in RH. I would also like to see the remaining reviewer points addressed in the final version, plus a few very minor comments from my side, as listed below.

To leave all options open, I will flag this as a major revision, but it does not necessarily have to go through yet another round of reviews. Thank you for your understanding and I look forward to seeing the paper published.

Best regards,
Stan Schymanski


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Minor comments by editor

L18: 'derivative' can be confused with the mathematical derivative. Maybe better: 'and the other is a derived PET measure that includes...'

L22: 'rate of'

L298-299: Please include references for the Pen-Pan model and the Penman equation.

L301: Better: '...which is a physically-based formulation of transpiration, considering the effect of stomatal resistance'. (It is not just a measure of atmospheric conditions, but contingent on canopy properties. Therefore your present statement could be misleading.)

L348: Is this the aerodynamic resistance for the 'reference crop of 0.12 m height'? Please specify.

L372-374: This is back to front. Increased air humidity usually causes stomata to open, also according to Lange et al. (1971). The more likely mechanism is that the vapour pressure within the boundary layer of a wet leaf is nearly saturated, suppressing water diffusion through stomata. The reason why Ishibashi and Terashima (1995) found stomatal closure in response to leaf surface wetness is likely not increased air humidity.

L394: Better: 'the number of days with snow cover'

Dear authors,

Thank you for embracing the reviewer comments and further improving the paper. Your responses and edits read very well, but I will send it out to Referee #2 one more time for a final comment.

Best regards,
Stan

Dear authors,

Thank you once again for your creative consideration of the reviewer comments. In this final review, the reviewer found a few more problems and suggested a few more changes that will likely improve the manuscript further. I added a few additional comments below. While the reviewer referred to the tracked-changes document, in my below suggestions, I refer to the updated document.

I am not sure I would agree with the referee's strong opinion about relative humidity being constant as the climate warms, as this may only apply over the oceans (see the wording in Schneider et al., 2010). However, I do agree that it is difficult to separate the effects of air temperature and humidity and therefore I wonder if it might be beneficial for the reader to see attribution based on assuming constant absolute and relative humidity as well as constant vapour pressure deficit, accompanied by a short discussion of the interdependency between air temperature and humidity.

I would like to re-emphasise the reviewer's point about inconsistent consideration of air temperature effects in the radiative component. On L347-350, you explain that the available energy (A) is computed as absorbed shortwave plus absorbed downwelling longwave minus emitted longwave, assuming that surface temperature is equal to air temperature. Obviously, replacement of surface temperature by air temperature is a gross simplification and it needs to be pointed out clearly that this may lead to artefacts. For example, on L591, you explain that increasing air temperature "decreases the radiative component (due to increasing outgoing LW radiation)", whereas a few lines later you clarify that "downward LW radiation is also proportional to the air temperature so that increases in downward LW broadly cancel the increasing outgoing LW radiation". My impression is that the net effect of air temperature on the radiative component in your analysis is likely an artefact of the simplifications inherent in your estimation of incoming and outgoing longwave. Although it may be justifiable, in the context of previous studies, to present the results as you did, I would urge you to mention this problem prominently in the description of the results (e.g. L633) and in the discussion. See also the referee's comment about L562-563, and his proposed way of considering the problem in hess-520-referee-report-1.pdf, attached to his review. I quite like the idea of first presenting results based on common methods and then present a new set of results based on an improved method, accompanied by a critical discussion of the approach. I leave the choice up to you, but the paper definitely needs an adequate discussion of the deficiencies in the longwave calculations due to lacking knowledge about surface temperature.

I am also a bit puzzled about the derivatives in Appendix C, as mentioned below. Could you please check that they are correct (especially wind speed) and explain in the paper how they were obtained? If they are not verifiably correct, this could shed doubt on the whole attribution section.

I hope that the remaining issues can be addressed easily, but just in case another review may be necessary, I am marking it as "reconsider after major revisions", as also suggested by the reviewer.

Best regards,
Stan

Additional editor comments:

L323: double word: "that that"

L 589-592: I would firstly remove the comment that increased air temperature increases the aerodynamic component of PET "as it makes the air
more able to hold water", and secondly clarify that the decrease of the radiative component is due to the assumption that surface temperature equals air temperature, which is a gross simplification. The effect of air temperature on PET (or ET) is through the surface energy balance, by its effect on sensible heat flux, as explained in Schymanski & Or (2016, PCE 39(7): 1448-1459). Given the simplifications about the surface energy balance in this study, I would be careful not to over-interpret the results. It is probably too late now to suggest removing the distinction between radiative and aerodynamical components, but I really think that the reader would benefit from a critical discussion of this distinction given the simplifications used here and elsewhere in the literature.

L471: You mentioned that you would adopt the wording proposed by G.P. Weedon here, but have not done so. Was this forgotten?

L614: "... to consider relative humidity (R_h) as the independent variable." I propose to add "as" so that the sentence does not imply that RH is indeed an independent variable.

L628: The reference to Jenkins and Dai is probably misplaced here, as the reviewer pointed out.

L700: Echoing comment by G.P. Weedon: Please mention the magnitude (and confidence interval) of the trends seen in this data set.

L720: As the referee pointed out, something went wrong here with the references. Please fix this.

L833: Eq. C1 appears wrong to me, as r_a is a function of the square root of wind speed, so the derivative is not complete. Could you also describe the steps that led to the derivatives in C2-C7? I wasn't able to follow the derivations.

Dear authors,
Thanks a lot for your detailed responses and clarifications. I think that the paper is in excellent shape now, but before publication, I would like you to double-check that Fig. B3b) is correct, as it is very different to the one in the previous manuscript, where most of the area was marked as having a significant negative trend in RH. Could you also update the data under the assets tab? It says "This dataset has been withdrawn and has been superseded by..." I am a bit confused, as I thought that the doi refers to a static data set. If it keeps getting withdrawn and superseded, reproducibility of your research may not be guaranteed after a few years, which would defeat some of the purpose.

I would also very much like to encourage you to publish the code you used to extract the data and perform the computations leading to the results in the present paper. This is not a formal requirement by HESS (yet), but I am convinced that some readers would greatly benefit from it.

Thank you on behalf of the readers.

Best regards,
Stan

Dear authors,
Thank you for the final clarifications. The reviewer is Jack Scheff and he is happy to have his reviews credited to him. Should this not get done during the final typesetting process, could you let me and/or your contact at Copernicus know? Thanks a lot!

Best regards,
Stan