Review of “Comment on "A theoretical upper limit for offshore wind energy extraction" by Simão Ferreira et al. (2026)” by van der Laan and Watson.

Overview:

van der Laan and Watson have provided a careful and technically rigorous critique of Simão Ferreira et al. (2026) by clarifying the interpretation and the methodological robustness of the proposed “theoretical limit” for offshore wind farm capacity factors. Van der Laan and Watson raise substantive concerns that significantly affect how the original results should be understood and applied.

Most importantly, van der Laan & Watson (vdLW) argue that Simão Ferreira et al.’s (SFLS’s) work cannot be considered a theoretical or universal bound analogous to the Betz limit. I strongly agree with vdLW that “the proposed limit … is not a theoretical limit … but a model limit ….” The SFLS derived capacity factor limit depends explicitly on modeling assumptions (turbine spacing, the treatment of finite wind farm effects). The language used by SFLS risks overstating the generality and physical inevitability of their result. More precise language would be “a model dependent upper bound under specific simplifying assumptions” rather than a “theoretical limit” which implies a fundamental constraint on wind energy extraction.

vdLW carefully examine the finite wind farm correction of SFLS and show that the correction method is ad hoc and insufficiently documented, that it is not reproducible without subjective interpretation. vdLW give a good-faith effort to develop (and document, and provide the python code via zenodo) an effort to provide an automated method to replicate the SFLS approach and demonstrate the insufficiencies of that method, further emphasizing that the SFLS approach is not reproducible. Further, they show clearly in Figs 5 and 6 that the SFLS model is highly sensitive to this parameter.  I recommend this important comment for publication in Wind Energy Science.

Major comments:

1. My main criticism of vdLW is that this comment is not critical enough of the overall premise of SFLS. Wind farm performance cannot be reduced to a single deterministic relationship without careful treatment of atmospheric variability and spatial heterogeneity; this point is not made in the carefully circumscribed comment.
2. vdLW correctly point out that SFLS's validation of capacity factors not only includes wake effects, but also grid losses, curtailment, and turbine availability losses (lines 187-190), but they could emphasize more clearly the impact of incorporating all these other losses into what SFLS label as wake effects.
3. vdLW do not comment on the implication of the large scatter in their Fig 6, which it seems might actually suggest that a more rigorous (or at least reproducible) approach than that given by SFLS would imply even more losses, which might argue that national policies overestimate possible capacity by an even larger margin. I recommend that they address this possibility in their conclusions, rather than simply saying that national policies are “difficult to assess.”

Minor comments:

1. Figure 2 has both red and green, which would make the bars difficult for colorblind readers. I ran the image through the WES-recommended https://www.color-blindness.com/coblis-color-blindness-simulator/ and recommend they choose different colors.

The manuscript under review presents a comment on a publication by Simao Ferreira et al. published earlier in 2026 that raised some attention also outside the academic community. Van der Laan and Watson – i.e., the authors of the comment – raise and elaborate on a number of concerns that may highly impact the interpretation of the findings from the earlier study. Overall, I believe, it is very relevant to raise these concerns and discuss them at a proper level in the community. The public discussion in Wind Energy Science confirms this but also shows that the comment may not be complete (and without shortcomings and misinterpretations) as commented by one of the authors of the original work. Considering this and several more structural shortcomings (see below), I am of the opinion that the “comment” under review should not be published in its current form and therefor suggest a rejection. This is not to stop or hinder the critical discussion of the previous study but rather to ask the authors to find a more comprehensive and diligent way of doing so.

Specific review comments:

[rather a formal aspect] Checking the acceptable manuscript types for WES (https://www.wind-energy-science.net/about/manuscript_types.html), I would expect a peer-reviewed comment only as a comment to a paper published in the same journal. As the two journals in our case seem to differ quite a lot in various aspects, I believe another manuscript type might be more appropriate here (e.g., a research article repeating more of the original work and describing the made amendments in event more detail, or a brief communication focusing on the impact of the previous study it is suggested shortcomings.)

[abstract] The abstract is very short and mentions “a number of concerns” and the single conclusion on the previously proposed “theoretical limit” only being “a model limit”.  I’d suggest that the authors detail this a little further – e.g., if this is the conclusion, what is their specific suggestion / next step? Is the previous study shown to be wrong or the results just associated with a higher uncertainty? The authors need to be more specific here.

[l 16] Interviews regarding the previous findings are mentioned, and it seems that the publicity around the original study has been the driver for the authors to draft their comment. Though this seems very obvious, it is not mentioned explicitly in the manuscript. I’d suggest that the authors are more specific on this aspect.

[l 19] “complex” (in “complex models”) is not specified properly here, but it seems that the authors refer to mesoscale models like WRF as a better truth. This should be further detailed here – not least because also mesoscale models / simulations depend on specific model assumptions and wind farm parametrizations that should not be considered as a (high-level) standard solution.

[p 2] The specific concerns are introduced in detail before introducing the basic details of the model and its application. This is not optimal as it requires the reader to have read the original study in great detail and depth beforehand. I recommend to the authors to find a better way of introducing their list of concerns.#

[l 63] k=2.4 is mentioned here, but it is only stated in l 72 that Simao Feirrera et al. used this single value for k in their study. This detail should already be mentioned at the first location.

[Figure 3 / 4] For both figures, “model results” should be specified further – which model here?

[ll 192] The sentence lists four wind farms but states them in pairs (which becomes clear when reading the sentence twice) – this is a bit confusing. I’d suggest to first list all four wind farm, and then explain the issue about the pairs.

[Figure 5] It is very hard to differentiate between red and pink symbols – please use another colour.

[l 204] “possibly due to differences in model implementation” is a very vague formulation – the authors should be more specific about their assumption / suspicion here.

[l 214] The statement “makes it impossible to draw strong conclusions about a limit for finite wind farms” seems key to the comment and requires further elaboration. I understand this is linked to the observed scatter – but where should we draw a line between possible / impossible? I do not say that I disagree with the authors here, but I strongly suggest to be more explicitly here and give more reasoning.

[ll 224] The statement in the conclusions “it is not trivial to use ..” is gain a hint that needs further elaboration. Generally, I feel, the authors must find a better balance between criticizing the original study for their approach in the interpretation of the results and correcting the technical approach behind that.