The manuscript is well written, logically structured, and clearly present the novel results. I have only a few rather minor comments to the study and its presentation.

Introduction in general. (1) Could you indicate clearly the research questions of your study; and (2) briefly present the structure of your manuscript?

Lines 75-80. There is rather rough transition to DNS results, please rewrite the text. 

Line 89. Wind is a projection of velocity on the horizontal plain, there is no "wind velocity", please correct.

Line 89. Why \Theta is bold, is it vector?

Section 3. Line 175. The paper would benefit from the Table with summary of all DNS experiments and their parameters.

It is also useful to have a Figure with the mean profiles of some DNS runs.

Line 202. What is "a rational regression model"? What software was used to obtain the regression? This is non-linear regression, what is the method to fit the coefficients? What are confidence intervals for the coefficients?

Figure 3. There are much more gray dots than red dots, why? Does the scatter in the gray dots mean that thickness of the transitional sub-layer was different in different runs. It would be useful to have a look on a few DNS run results.

Figure 4,5,6. What are statistical significance of the presented regressions. Scatter is rather large there, what is R-square (explained part) for these approximations?

Conclusions. It would be helpful to have a brief summary of the obtained closure with all values of coefficients summarized in a Table.

Code and Data. It is reasonable to make available all data used to plot the figures as well as the mean characteristics of DNS runs and mean profiles through a data sharing facility, e.g., ZENODO or similar. 

My criticism of this paper is strategic: it continues the long, largely unsuccessful two centuries of grappling with turbulence, closure and dissipation, particularly in the atmosphere. Within that genre, it is an acceptably good paper. However, recent perspectives, referenced in my review, need to be thought about.

This manuscript aims to provide additional insight to the effects of stratification on turbulence properties and consequences for how we model those. The results are based on DNS data and show some promising results and valuable discussion, however, there are some odd choices in the analysis that result in more confusion than clarity. Furthermore, the abstract and introduction includes discussion of conditions up to extreme static stability which the results of the paper does not provide results for. At the end of the manuscript (line 310) it is noted that the DNS experiments were limited to gradient Richardson numbers up to Ri=0.2. This statement does not align with the Figures that presents data up to z/L = 5 which is confusing. This discrepancy goes to the heart of my problem with the analysis which is the introduction of performing the analysis using z/L as stability parameter which is just introduced without proper motivation on line 145. At the end of the manuscript, the authors then advocate to go back to a Richardson number (in this case the gradient Ri) with the motivation “for practical reasons”. I would like to see the analysis performed using Ri as the stability parameter throughout which I anticipate would provide a more straightforward analysis. Furthermore, I dislike the extrapolation outside of the DNS parameter space, for example the exponential growth far outside the range of the DNS results in Figure 6d. Presenting the results in this way discredits the results. In conclusion, the manuscript needs considerable rewriting before it can be properly judged for publication.

Line 25: There is no analysis of extreme static stability presented.

Line 144: There is no motivation for using this conversion from flux Ri to z/L (which is a stability parameter and not a stratification parameter). I understand from reading the Acknowledgements that Prof Zilintikevich was instrumental for the project, maybe this remains as one of his ideas. However, if it does not make sense for the continued analysis, it should be removed. That would be in the spirit of Sergej, whom I knew and also worked with.

Line 152: It is not correct to write “empirical validation”. First DNS data is not empirical data, and second, the data is used for evaluation not validation.

Line 171: More details on how the prescribed Dirichlet boundary is imposed to maintain the stable stratification is needed.

Line 172: Why did you chose to fix a value of the molecular Pr number to 0.7. What is that based on?

Line 183: When reaching the end of this description, there are still missing information on how the DNS experiments were conducted. How many simulations? Initial conditions? Time step? At what stratification? When did the simulation reached statistical steady-state, to what accuracy? Again, it is stated “turbulence up to extreme static stability” which is not that case. How do you know that you are resolving all dissipation time scales? Do you have any numerical diffusion? The experimental parameters could be summarized in a Table. It would also add to the manuscript if the various experiments were color-coded in the Figures so they can be identified.

Line 187: Is it correct to interpret this statement as buoyancy is a dissipative term in stratified conditions?

Line 197: It is really not clear to me why you choose to plot the results as function of z/L when you have Ri_f in the equation. Furthermore, I think it would be good to remove the near-neutral DNS results as they are not credible anyway in all figures, that would lead to improved visibility in the various panels. The fitted line in Figure 1 cross z/L = 0 at the value 0.2, is that a given? Do you have neutral DNS to constrain that?

Line 199: Why to you propose a ration of two first-order polynomials? That is a quite advanced fitting, did you try simpler representation of is the proposition based on any theoretical argument?

Figure 2: The labels are very unclearly written, or unnecessary complicated.  I assume you are dividing with the whole left part of Eq 31 but the label it is not clear.

Line 252: Would be good with some references here for this discussion, there are empirical results for how asymmetry varies.

Figure 5: Could be interesting to see how this would fair with other assumptions for Az. The DNS results are quite variable.

Line 281-285: See discussion above regarding the stability parameter, the discussion here is not very insightful.

Line 286: Why is the function a polynomial of the 5^th order?

Line 310: I do not understand why you show results that are outside of what the DNS results support. Overall, the figures need to be of better quality.