Referee's report on the paper

 Turbulence Kinetic Energy dissipation rate: Assessment of radar models from comparisons between 1.3 GHz WPR and DataHawk UAV measurements

Hubert Luce, Laskhmi Kantha, et al.

** pls check -  Is "Laskhmi" spelled correctly??

This paper combines a nice concise review of the current state of play with measurement of turbulent energy dissipation rates in the atmosphere by in-situ and radar methods. It is backed up by some good experimental data as well, and contains nice side-by-side radar/in-situ comparisons.

I applaud the effort, and will recommend publication - but subject to a few caveats.

First, there is some lack of clarity in the terms TKE and ∈.     The abstract seems to suggest that they are almost the same, but one is a total energy and one is a dissipation rate. But in line 120 and elsewhere they are treated as different entities - maybe I am misinterpreting something, but I think TKE and e need to be more carefully defined.

A more serious error occurs in lines 136 to 142 - and especially line 142, where it says

"In essence, there is no contribution from an anisotropic buoyancy subrange." The theory of Hocking (1983) does NOT assume this. The factor of 1/2 in Hocking (1983), eq, (2) comes from a crude assumption that the radar receives half of it's v^2_rms from the inertial range and half from the buoyancy range. (In fairness to the readers, this was not fully explained in the original paper.)

I would ask the authors to please look at Hocking et al. (2016) [Atmospheric Radar:  Application and Science of MST Radars in the Earth's Mesosphere, Stratosphere, Troposphere, and weakly ionized regions", Cambridge University Press, 2016.  ISBN 9781316556115, DOI: https://doi.org/10.1017/9781316556115], pages 407-408.

The more advanced theory presented there allows for a variable contribution to v_rms from BOTH the inertial range and the buoyancy range.

So the theory ascribed to equation (2) of the current paper is not the latest - in a more complete form, it should include this factor F - see the pages indicated above. 

Indeed it might be possible that this fraction F could be allowed to be dependent on ∈, which could allow better consolidation between the theories presented in the paper under review. Physically, this is not unreasonable - for example, more intense turbulence could more rapidly destroy the stratification,  allowing for larger isotropy at larger scales - even into the buoyancy range --  and this would allow a larger contribution to  the vertical RMS velocities from the buoyancy range, reducing the fraction F.

Indeed the behaviour of this "buoyancy range" is not fully understood at all - it is clear that turbulence here is anisotropic, with suppressed vertical velocities relative to the horizontal ones, but exactly what this ratio is is quite unclear. It also leads to huge levels of confusion relating to the so-called "buoyancy scale" of Weinstock and the similar but different" Ozmidov scale".

So I ask the authors to at least refer to this later work, and incorporate this fraction F into discussions. They may choose to say that "for a fixed value of F" it does not agree with the eq (1), but it might reconcile better if F varies with ∈, and might allow further insight into why eq. (1) seems to work so well (which is still a bit of a mystery, as discussed by the authors in section 5.1). 

Indeed  (jumping ahead a bit!) I found section (5.1) quite unhelpful in this regard, and I sense that the authors have similar issues, so it might be useful here to consider further the relative roles of vertical velocities in the buoyancy and inertial ranges, which relates in turn to F. (remembering that most of the issues here arise because the pulse-length and bean widths are right around the buoyancy scale)

Another point to bear in mind in regard to section 5.1 relates to Figs. 7.12 and 7.13 of Hocking et al. (2016). While it is easy to believe that the Datahawk is somehow more "perfect" than a radar, as it samples at a single point in space, determination of a spectrum (or alternatively an autocovariance) function requires a finite length of time, and in that time, the datahawk moves, and additionally the  mean wind blows different regions of space across the datahawk as well, so the datahawk also has a spatial sampling across many tens of metres, just like the radar. This may also relate to the "70m" scale. 

Returning now to section 2, the discussion in section 2.2 is great.

However, I do note some inconsistencies in the text as to the terms Ri and Rf  - in places they  are written as subscripts (R_f) and sometimes not. Please decide which is best.

Section 3 is straightforward, though the authors refer to 59-s data sets and 1-min data sets, which I assume are one and the same (??).

Section 3.3 -- Ozmidov scales and Thorpe lengths are discussed, but they also relate to Weinstock's "Buoyancy scale" and there is a factor of 10 (2π/0.6) difference here - may not be relevant in section 3.2 but certainly relevant in a general context.

 Line 210 - please more formally define "TKE" and distinguish it from e - maybe it was done earlier(?) - if I missed it, I apologize - but I think the distinction needs to be clear.

The case studies (section 4) seem well documented.

Section 5.1  - see my earlier comment.

Figs 5 and 6 - note that references to the ∈_N formula assumes F=0.5 (see earlier)

Fig 6 - please add values of R and P, as you have done for Fig. 7

Line 392 - Terns like "cst" appear -  I am not clear what cst means!?  I could not find a definition.  Please clarify.

Page 15 - various limitations of ∈_N are discussed, but remember these all assume a fixed value of F, so it must be made clear that this is the simplest verison of this model, not the most complete.

Conclusion - great paper, nice review, nice data, but please recognize that the latest version of the model for Eq. (2) has NOT been used, and the authors have assumed a fixed fraction F (relative contributions of inertial and buoyancy scales). If the authors continue using the current discussions, they are obliged to recognize verbally that they have assumed a simplified model with fixed F, which may not be realistic. Using the 1983 version of the theory pertaining to Eq (2) and not considering the 2016 version is a bit unfair.

The case of the radar  resolution being much less than the buoyancy scale has also been discussed in Hocking et al. (2016) pages 409-411, and of course also in the paper by Kantha et al., (2017),and all parties agree that in such cases ∈ should be proportional to vrms^3 - it should be noted that this is true, and the complications discussed above arise from the cases where the pulse -length exceeds the buoyancy scale (or equivalent) and where data-lengths are not too long.

One positive point from this paper is that it seems we as a community are getting better at measuring ∈ values - contrast this to Fig.1 of Hocking and Mu, in which even the definitions of "light", "moderate" and "heavy" turbulence differed by factors of 10 and more, depending on the author. Despite all the concerns in this paper, Fig. 6 shows that between ∈ = 10^{-4} and 10^{-2}, all models agrees to better than half a decade (factor or 3) nowadays.

Review report of

Turbulence Kinetic Energy dissipation rate: Assessment of radar models from comparisons between 1.3 GHz WPR and DataHawk UAV measurements

By Luce et al.

Summary of paper:

This paper presents some derivations of turbulent energy dissipation rates epsilon in the lower atmosphere with in-situ and radar techniques. The authors give a nice review of the algorithms to estimate epsilon mostly used in the community, although some of them have been assessed and some are used with different hypotheses. Based on the analysis of dataset on a campaign-basis, they further estimate epsilon and compare the results derived from different techniques for case studies as well as for statistical analysis.

General comments:

The research topic of turbulence detection in the atmosphere is very interesting and important and certainly relevant to the readers of AMT. The authors have a unique dataset with in-situ and remote sensing instruments at their disposal that are certainly valuable for the corresponding research. The manuscript is well written and organized and of course deserves to be published. However, there are several points should be clarified before publication.

Different probing techniques have different spatial coverage: in-situ instrument for a point and radar for the cross section of a volume. The necessary discussions or significance test should be given when one compares the derived epsilon from different techniques. Otherwise, the resulting consistency seems to be coincident, especially for the case studies.

For any study of turbulence intensity estimate, it is very important to describe the details of each steps. Each technique suffers from different instrument limitation. The error bars for the measurements are very important and may play a determining role in the results. The discussions on the error sources for each instrument, in my opinion, are very important and necessary.

It is mentioned in the manuscript that the value of c (i.e. the ratio of L_O to L_T) is tricky by applying the Thorpe analysis. Different authors used different c values for their calculations. This is because the experimental validations for this ratio in the atmosphere are very sparse. Based on several balloon flights, Schneider et al. (2015) directly checked the relation of L_O and L_T and they found the distribution of c^2 covers a very broad range of 2 orders of magnitude. In my opinion, this work (https://doi.org/10.5194/acp-15-2159-2015) is worthy to be referenced in the current manuscript.

In this manuscript, the authors give a nice review of the different algorithms to estimate epsilon with a large number of symbols. For ease of reading, I recommend the authors to add a list of symbols (maybe also including abbreviations).

Typos and suggestions listed as follows (but not limited to):

1. Line 14, does “ASL” mean above sea level? It should be clarified elsewhere.
2. Line 60, N is B-V frequency, not N^2.
3. Line 79 and line 84, the references should be accurate (Hocking, 2016 and Hocking et al., 2016).
4. Line 79, the sentence “… Appendix of L18” is misleading. Please check.
5. Line 109, what do the arrows mean here? (And the arrows used elsewhere) Please clarify them or describe in text.
6. Line 122, please reconsider the subscripts, like Ri_S and Rf or R_f elsewhere.
7. Line 123, epsilon = P/G – B;
8. Lines 140-141, please add references?
9. Line 156, does AGL mean above ground level? Why do the authors use both ASL and AGL?
10. Line 158-159, please consider to add any reference for the processes or algorithms to remove outliers?
11. Line 267, Figure 12 not found. Please be sure.
12. Line 320, please remove “4.1.3 Comparison with epsilon_T”
13. Lines 335-336, please rephrase the sentence (Depending on …).
14. Line 362, please rephrase the sentence with more clear expression.
15. Line 392, what does “cst” mean? Constant? It is also used elsewhere. Please clarify.
16. Line 426, what is P test? Please add references!