The manuscript presents a valuable and as far as I am aware unique analysis of the benefits of applying a combination of wake steering and wake mixing on turbines in a large-scale wind farm. The analysis is executed using a low-fidelity engineering model, which is both the strength and the weakness of this work.

The manuscript is a valuable addition to existing research in the field of WFFC. However, I believe the manuscript in its current form has some significant shortcomings that need to be addressed before publication.

I was torn between recommending minor or major revisions, so please do not interpret my final choice to mean that I do not like the manuscript. I actually really liked the manuscript, which is why I wrote such an extensive review. I believe this manuscript is good work that has the potential to be great work if some of the shortcomings are addressed. I do not doubt the authors’ ability to address my comments though, and when they do, I will gladly recommend this manuscript to be accepted.

First and foremost, I believe that the fidelity of the engineering model substantially puts into question the reliability of the final results. I have the following concerns with the engineering model that I feel need to be addressed or at least mentioned:

1. The model is used (far) outside of the space it is tuned for. As far as I can tell, the model is tuned for one specific boundary layer condition, one wind speed, one TI percentage, and only for up to three wind turbines with only one specific spacing. It is specifically NOT tuned for partial wake overlap, deeper arrays, or control actions implemented on downstream (waked) turbines. However, the case study does involve all of these conditions. This daisy chain of extrapolations makes that the uncertainty of the model, which is not quantified in any way in the paper, likely far exceeds the reported AEP gains for the case study wind farm. The fact that the model was tuned without any of these dynamics should explicitly be mentioned throughout the paper.
2. I know neutral boundary layer conditions are common in the North Sea, but it is a significant simplification to consider this representative of the year-round conditions in the case study wind farm. The same is true for the wind speed and turbulence levels. I can see how 10 m/s and 3-6% might be average for the North Sea, but “average” is not the same as “representative”. I recommend adding a Weibull distribution of the wind speed measured at the wind farm, accompanied by the TI range for each wind speed bin. This will likely show that the TI is generally higher at low wind speeds, when WFFC in general, and the helix specifically, is most effective. Therefore, by tuning for a relatively low TI, you might overestimate the benefit of the helix, which should be mentioned. You do say you use the Weibull distribution to calculate the AEP, so regardless of this point, I feel like a figure of the distribution should be added to the paper.
3. Currently, the flow model validation is limited to two figures tucked away in the appendix. This should be a major part of the paper, as the reader needs to be able to assess the fidelity of the model to put any trust in the reported findings. The results in Section 3.1, using the 2-turbine layout, are perfectly suited to compare the engineering model with LES data. You should be able to produce LES equivalents of Figure 4 at different control settings (using rotor-averaged wind speeds) to compare with the model. This is the “simplest” case that is basically exactly what you tuned your model for, so this provides a floor on the error that should be expected for the wind farm case. I believe this needs to be added to the revised manuscript.
4. I understand that LES runs are timely and costly, so although I believe more simulations at different conditions are necessary to sufficiently tune the model, I respect that you have to deal with a limited amount of (computational) resources. However, this should be mentioned as a limitation of the study much more explicitly. It should be made (more) clear to the reader that the case study far exceeds the conditions for which the model was validated, and that the results should be interpreted accordingly.

Other major comments:

1. The quality of the written text is fair, not great. Many sentences do not flow naturally, the order of words is sometimes unintuitive, the interpunction is not always logical, and the choice of words is not always fluent (and this is coming from a non-native English speaker). In my opinion, it is good enough, the manuscript is certainly understandable in its current form, but I would personally strive for a higher standard. I therefore recommend having the manuscript reviewed by a professional editor or a native English speaker.
2. I would suggest changing the title of the paper to improve expectations. When I first read the title, I assumed 1) that wake steering and wake mixing were going to be applied on turbines simultaneously (about which I was skeptical), and 2) that different wake mixing strategies would be studied. I quickly learned that neither was the case, but I would suggest changing the title so that it better reflects this and better guides the expectations of the reader.
3. Why do you use the IEA 22MW turbine? Unless my Googling skills betray me, the case study wind farm HKN is equipped with 11MW turbines. However, you seem to conveniently leave this out of your manuscript. Wouldn’t it make much more sense to use, for example, the DTU 10MW reference turbine (or even the IEA 15MW turbine), as it is much closer in size to the actual wind turbines used? I assume you had a practical reason to use this specific reference turbine, which is understandable, but should be justified. The subsequent scaling of the whole farm adds another layer of uncertainty to the already highly uncertain final conclusions of the paper. Did you also scale the wind speed to correspond to the same point on the turbine wind speed-power curve?
4. You do not mention whether controller behavior changes between region II and III. I therefore assume it doesn’t. However, up until now, as well as in your LES cases, the helix approach is only studied in region II. If your study does not limit helix to region II, you should mention this as an additional degree of uncertainty.
5. I really like the approach taken to consider the uncertainty in wind direction using probability distribution. I think this might be the most valuable contribution of this paper. However, I do have a few smaller remarks with respect to this approach:
   1. I assume this uncertainty does not propagate downstream, is that correct? In other words, you only consider unintentional misalignment for turbine power production, not for how it might affect the wake (unintentional wake steering). I understand that including this would be much more complicated, so I do not expect you to add that, but I think it is worth mentioning as this could further affect the performance of WFFC, specifically wake steering.
   2. Did you consider using a non-zero mean for the probability distribution? I believe that sensor bias is a common issue for wind turbine anemometers, so this could be relevant to study. How might that affect your findings?
   3. Why did you choose the uncertainty levels of 2.5 and 5 degrees, if literature shows that values of up to 5.25 degrees are observed in the field?
   4. Finally, and this is my only major objection to the method used, you assume different levels of uncertainty, but at the same time, you also assume perfect knowledge of the level of uncertainty when choosing the control actions. However, in a real wind farm, you do not know the level of uncertainty a priori, and it usually changes over time. How would your results change if you do NOT have perfect knowledge of the uncertainty? I would really like to see a section added to the paper where you use the LUT for 0 degree uncertainty, but then implement it on the case with 5 degree uncertainty, and compare that to the case where you had perfect knowledge (for both the 2T and the HKN case). I feel like this better represents how WFFC is implemented on real wind farms, and requires only a limited additional simulation effort. This would in my opinion better show the effect of wind direction uncertainty on AEP than your current approach.
6. Given all the uncertainty regarding the reliability of the AEP gains as addressed in multiple points above, I would seriously consider not mentioning the specific percentages at all. I think it would be better to stick to the more robust RELATIVE conclusions that wake steering works better with no WD uncertainty, helix with WD uncertainty, and a combination of both works best. That is in my opinion still a valuable finding, that is much less likely to be rebuked by future research using a better / more thorough methodology. At the very least, I would remove the percentage claims from the abstract and conclusions sections, or add lengthy caveats mentioning all the layers of uncertainty surrounding these numbers.
7. I do not fully understand why wake steering performs as badly as it does in your simulations when WD uncertainty is considered. I would expect a more significant drop than for the helix approach, as is observed, but I hadn’t expected the difference to be this big. This is also supported by section 3.1, which is much more in line with my expectations. I think this surprising result, and discrepancy between a simple 2-turbine setup and a complex 69-turbine wind farm, deserves deeper digging into. If these results are to be believed, the simple 2- or 3-turbine setups commonly used in assessing WFFC are actually terribly bad at predicting the benefit of WFFC strategies. That would be a very significant finding. However, as the analysis of this discrepancy is limited in the current manuscript (and my limited belief in the fidelity of the model), I am not sure if I can fully trust these results.
8. I would be very interested to see where the wind farm AEP gains originate from. Would it be possible to add a plot showing how much each turbine within the farm gains/loses power with respect to baseline?
9. Related to the above, figure 7b indicates to me that a significant part of the gain of helix is obtained by using it on downstream turbines. As you briefly mention yourself in the discussion, this is still very much uncharted territory and requires synchronization. Your model is also not tuned for waked turbines using the helix approach, not to mention waked turbines where the upstream turbine is also using the helix approach. I therefore feel like I need to know how much of the AEP gain can be explained by waked turbines using the helix. Could you please run a simulation in which only freestream/upstream turbines are allowed to use the helix, and compare the AEP gain with the situation in which all turbines are allowed to use it? I do not think this simulation needs to be added in detail to the manuscript, but I do think it is important to quantify what portion of the AEP gain comes from downstream turbines using the helix approach.

Minor comments:

Line 2: rather THAN the output

Line 2: an established WIND FARM FLOW CONTROL approach

Line 4: you should define/explain the helix here, or at the very least specify that this is the wake mixing strategy that you are studying in this paper.

Line 19: I would say wake steering is THE most effective solution, or at the very least the most established solution.

Line 30: “These concepts have …”, I think you mean the helix here, as all the citations refer to helix studies. If so, it should be singular (“This concept has …”)

Introduction: I know this is a personal preference and I wouldn’t say it’s wrong, but I don’t love the use of present perfect tense throughout the introduction. You are at least consistent, but I would personally prefer past tense or even present tense (“Citation A showed that …” instead of “Citation A has shown that …”).

Line 43: It is fair to say that the analysis limits itself to two-turbine arrays, but in your study, you also only do LES for three-turbine arrays. I would therefore argue that your findings have similar limitations.

Line 80: “… in reaching the global optimum.” Please add a source for this claim.

In general: Why did you choose to specifically study only the helix approach and not DIC? I have no issue with the choice, but it couldn’t hurt to justify it.

Line 90-94: Make the contributions listed here full sentences please. Also, I wouldn’t split them up into two lists, the “additional contributions” are in my opinion just as much contributions as the main ones.

Line 97-99: Use “Section” or “Sect.”, but be consistent.

Line 106 “The effect of wake steering …”: add “on the upstream/waked turbine”.

Line 130 / Appendix A: In my opinion, the process of tuning the model is fine to be moved to an appendix. However, the results of the tuning, i.e., how well your model matches the higher fidelity LES data, is very important in assessing the reliability of the results, and should be moved to the main part of the manuscript.

Table A1: “inflow”, not “infow”

Section 2.5: I would move this section forward, as I felt like I already needed this information to understand some of what was mentioned in previous sections.

Figure 3&4: consider trimming the y-axis, at least for the first two rows, to show a more relevant/zoomed representation of the findings.

Figure 7a: what is the downstream distance between the controlled turbine and the nearest downstream turbine in the 225 degree-sector where helix is implemented? How much does this downstream turbine benefit from the shown turbine using the helix? Does that correspond to the LES results?

Line 381-383: You only mention one of the many dimensions in which you are extrapolating LES simulations here. This section should include a much more extensive summary of ways in which you are extrapolating results.

Line 451 “with a specific focus on the helix technique”: a specific focus implies that you also looked at other wake mixing techniques, which you didn’t.

Table A2 (1): For tuning the turbine model, did you use LES simulations or standalone OpenFAST simulations? If you did the former, you could use these simulations to compare optimal values found with the pyWake model, at least in the case of a 2-turbine setup, to validate the match.

Table A2 (2): As part of the model verification, please provide a comparison of turbine powers between the 3-turbine LES cases and the exact same setup in pyWake. As mentioned above, this would function as a floor on the modeling error and helps the reader assess the reliability of results in the more complex case.

Appendix B: It seems to me that the current algorithm uses unnecessary repetitions of the same simulations. Perhaps that doesn’t matter since the simulations are cheap, but if that is the case, then why do you not take more iteration steps than the 3 mentioned in Table 1 to assure convergence? Furthermore, I am surprised to see that smaller values are found to be optimal for the helix method. How does this compare with the results from the LES simulations?