Review of "Estimating the technical wind energy potential of Kansas that incorporates the atmospheric response for policy applications" by Jonathan Minz et al. under consideration for Wind Energy Science

The authors investigate technical wind energy potentials under different wind park scenarios. They contrast the "standard" approach, which ignores depletion of atmospheric kinetic energy by wind parks, with explicit WRF modeling presented in a different study and a physics-based simple model called KEBA. The study focuses on Kansas. The authors find that the standard approach is not justified when huge wind parks are build and they argue that KEBA is a computationally tractable alternative to running highly resolved fluid dynamical simulations. 

Overall, the study appears as a fine model intercomparison study. However, since the authors repeatedly stress the policy relevance of their work, a more balanced perspective is needed to contextualize the results. This is because the suggested wind park cluster in Kansas is huge, even exceeding the current global installed wind park capacity by about 30%. 

Moreover, according to the SI of the manuscript, this paper has been submitted to Environmental Research Letters in 2021 (see KK2021_Readme.pdf available at https://edmond.mpg.de/dataset.xhtml?persistentId=doi:10.17617/3.78). I do not think that prior rejection elsewhere necessarily implies that the paper is not worthy of publication. However, I ask for an explanation of how the current version of the manuscript relates to the older one and how the earlier reviewer comments have been taken into account. 

I provide a list of additional major and minor comments below.

Major

- According to the Global Wind Energy Report 2023 (https://gwec.net/globalwindreport2023/), a total of 900 GW is currently installed on the entire planet. According to your Table 2, the studied wind park has an area of 112 000 km2. Using the upper end of the capacity density range (10 MW / km2), you suggest to install >1.1 TW in Kansas alone. That is, you suggest to install more wind turbines in a single US state than we currently have on the whole planet. Given how extreme this scenarios is, I am surprised that you do not discuss this at all. 

- Your calculation of LCOEs suggests direct real-world relevance. However, I am sceptical whether the results can be used in the real world because the scenarios are very extreme and the highly simplified (one small turbine only, a single massive park instead of multiple ones that allow for flow recovery, single hub height, rectangular shape, no directional dependence). Please provide strong justification or consider removing. I think that the paper would benefit from being framed as a model comparison without any immediate policy relevance other than "if you build very huge wind parks, think about modeling wind resource depletion".

- Lee Miller is listed as a co-author in the SI. Why is he not on the author list? What happened with the ERL submission? What has changed since then?

- Why is it justified to ignore wind direction and wind park orientation? Those have a strong effect on how important the impact of wakes are.

- l. 146: "using atmospheric conditions from May 15 to September 30, 2001. This period is considered to be climatologically representative for this region (Trier et al., 2010)" --> This is a very strong statement and I doubt that it is correct. You are saying that 4.5 months are representative for average wind conditions over 20-30 years (which is the timespan that is normally used to define climatologies). Please provide quantitative evidence as such a limited input sample might severely impact the validity of your results.

- In Fig. 3 how is it possible that the wind speeds and the capacity factors both decline linearly with W/m2 (which is installed capacity I believe...)? Are you sure that you are using the same x-axis for both? Since the relationship between them is non-linear, I don't see how both can be linear. Also this Figure is a good example that you need clearer axis labels.

- "This is likely because KEBA assumes a well-mixed boundary layer volume that is characterized by one effective wind speed, veff." --> I do not quite follow this argument. I think there are two elements that need unpacking here: 1) why is it justified to assume the same wind speed at all heights in the boundary layer? 2) Why is it justified to assume the same wind speeds at the 1st and the 1000th wind turbine in the wind park? In reality, winds strengthen with height and will weaken as air travels through the wind park. Please add an explanation why your approach is justified despite these concerns. 

- How are your results impacted by the choice of a wind turbine with relatively low hub height? Since mean wind speeds would be higher at, say 120m, wind speed reductions due to resource depletion might be less important if the turbines operate more often in the rated regime. I suggest to add technology uncertainty to your discussion of the limitations of the approach.

- Conclusion: "We conclude that the KE removal effect is the predominant physical influence that shapes technical wind resource potentials at the regional scale." I do not think that you have shown that. The dominant phyical effect is wind speed. You have shown that the KE removal effect becomes sizeable when capacity density and park are are both very large and that KEBA can be used to estimate it with some level of confidence (although the deviation from WRF remains sizeable as well and one could also questions whether WRF is the best ground truth)

Minor

- All slopes are missing units! For example, in lines 226 and 227 but also elsewhere. 

- Figure axis labels: Please add the variable name in addition to the units. The units themselves are not clear. For example, in Fig. 4, both axis have the same units (except a factor 10^6) but they have different meaning. This comment applies to almost all Figures.

- In the abstract, I suggest to cut down the introductory sentences to increase legibility (and make the paper more attractive to readers). Basically, I recommend to shorten lines 1-10 to maybe 4 lines or so. 

- In the abstract you write: "However, the depletion of wind resource or the reduction in wind speed scales with the total capacity installed within the deployment." I see two problems with this statement. First, it is unclear whether this is a result from the current analysis or a general statement. Second, I don't believe that it holds in general. For example, a wind park with 1GW capacity spread out over area A would not see the same depletion as 1GW wind park spread out over 100*A.

- l. 15 ff: not clear what the percentages refer to. Relative to what?

- The Introduction is generally of good quality. As a reviewer, I have nothing to critize. However, as a reader I would have prefered more conciseness.

- l. 41: you are missing a verb in this sentence

- "This effect is borne out in observation data" --> unclear what this means. 

- "The winds of the large-scale circulation and KE associated with their mean flow are predominantly generated in the free atmosphere by differences in potential energy due to differential solar radiative heating (Peixoto and Oort, 1992; Kleidon,

2021)."  --> suggest to define free atmosphere. And do you mean atmosphere or troposphere?

- Fig. 2: I like the idea of a conceptual figure. I noted a few things in this figure that you might want to change:

    - I would not use arrows to depict the boundary layer height because you use arrows to depict momentum fluxes.

    - The circular arrow behind the wind parks seems to suggest that a circulation cell forms during the day. I don't think that this is what you suggest.

- Which GCM are you talking about in Sec. 3.8?

- Figure 5 needs a legend that explains the different markers.

Point 1)

The study is one of many within a growing field, that is numerical simulations of large scale deployments of wind turbines.

It is therefore a bit surprising to notice that the authors are referring to rather small turbines, 3MW turbine from Vestas. With a hub height of 84 m. 

The state of the art for the win energy industry seems to have passed this some time ago. The systems are simply much bigger now.

This is raising the question if the algorithm proposed in the paper will work for systems with 10-15 MW (or even bigger) turbines and much higher hub heights.

Point 2)

Along the same line of reasoning: it is also a bit surprising to see that more than half the references are from 2015 or earlier. With only 2 from 2022.

Point 3)

In the study the production is calculated for a period of four and a half summer months. It is stated that this period is climatologically representative for the region. There is no quantitative argument for this conclusion.

Why is the winter period not relevant for a study where one main point is that there are differences between day and night conditions due to diurnal fluctuations in static stability and convection?

Point 4)

We don’t get an explanation for choosing an area of 112.000 km2, app. half the size of Kansas. The authors are stating that the electricity production of their wind farms is 3 to 5 times the total energy consumption in Kansas in 2018.

Point 5)

Obviously big wind mill farms have to be constructed in such a way that the individual turbines don’t interact too much with the neighbors. Therefore, one needs a method to make reliable estimates. 

And with a tight economy for the wind energy market is it not then necessary that the final electricity production is known as precisely as possible? And can the KEBA approach then compete with the “WRF” approach?

Some of the choices made in paper regarding for instance boundary payer heights must in all cases be adjusted to the local geography and climate.