A novel analytical tool to capture wind profile variability for wind energy assessment: fast, simple, and beyond state-of-the-art in complex terrain

van Schaik, Brandon Jacobus Adrianus; Baruzier, Alice Juliette; Loyer, Clément; Huwald, Hendrik; Lehning, Michael

doi:10.5194/wes-11-4125-2026

Articles | Volume 11, issue 11

https://doi.org/10.5194/wes-11-4125-2026

© Author(s) 2026. This work is distributed under
the Creative Commons Attribution 4.0 License.

https://doi.org/10.5194/wes-11-4125-2026

© Author(s) 2026. This work is distributed under
the Creative Commons Attribution 4.0 License.

Articles | Volume 11, issue 11

Research article

|

06 Nov 2026

Research article |

| 06 Nov 2026

A novel analytical tool to capture wind profile variability for wind energy assessment: fast, simple, and beyond state-of-the-art in complex terrain

Brandon Jacobus Adrianus van Schaik, Alice Juliette Baruzier, Clément Loyer, Hendrik Huwald, and Michael Lehning

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Final revised paper (published on 06 Nov 2026)
Preprint (discussion started on 30 Dec 2025)
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Status: closed

RC1:
'Comment on wes-2025-271', Anonymous Referee #1, 17 Mar 2026
Summary:
The paper presents a new analytical model accounting for the vertical variations in horizontal wind speed to assess wind turbine power production. The approach relies on the Taylor expansion of wind profile measurements in the rotor swept area obtained from Doppler lidar observations. Results from the analytical model are validated against OpenFAST simulations and measurements from wind turbines operating in the Gotthard Pass wind farm in the Swiss Alps. The topic of the manuscript is of interest since this method provides an estimate of turbine power production at a relatively low computational cost compared with other approaches. Moreover, the detailed knowledge of the turbine mechanical characteristics is not required, and the wake effects between turbines can be addressed by this new method. However, the manuscript lacks clarity, organisation, and rigour, which hinder its readability and reproducibility. More work is needed to improve the manuscript by addressing the following comments:
Major comments:
Key explanations are missing or not clearly formulated. While the Taylor series decomposition of the wind profile is well detailed, the complete methodology is not fully described. In particular, the extension of this decomposition to the wind variance profile is not explicitly explained. Furthermore, it remains unclear how this variance decomposition is used to predict turbine power output and how the power curves are obtained. All these points should be addressed in the revised manuscript.

Several points raised by the editor were not addressed in the manuscript. In particular, the suggested revision to the opening sentence of the abstract was not applied. Furthermore, while a few references were added, the proportion of self-citations remains high, and the paper still does not introduce or discuss previous studies focusing on alternative rotor equivalent wind speed formulations.

The current structure of the methodology section (section 2) is confusing. The analytical model is introduced (section 2.1) before the input data is presented. The OpenFAST configuration is split between sections 2.2 and 2.5, making it difficult to get an overall view of the numerical modelling approach. Moreover, the current section titles (e.g., "Analytical method", "Numerical method") are imprecise and should be more descriptive. Here is a suggested restructuring:

2.1 Wind profiles
    2.1.1 Idealized wind profiles
    2.1.2 Gotthard Pass wind profiles
2.2 Power prediction through analytical method
    2.2.1 Rotor-averaged cubic wind using Taylor expansion of the wind profile (which corresponds to the current paragraph before section 2.1.1)
    2.2.2 Turbulence modelling
    2.2.3 Power curve fitting (current section 2.1.1)
    2.2.4 Application to idealized and real wind profiles
2.3 Power prediction through numerical modelling (OpenFAST, current section 2.2 and a part of the 2.5)
2.4 Analytical model validation strategy (current section 2.5.1, to merge with the current introduction of the results and discussion part (section 3))

Minor Comments:
General comments on the manuscript (please refer to detailed comments below for details):
Units are written in italics throughout the manuscript, but should be written in normal font.

Units are sometimes specified in brackets in the text (e.g., line 83) but omitted elsewhere (e.g., line 267). It should be consistent throughout the manuscript. I recommend removing the brackets as this improves readability.

Some formatting issues create large blank spaces in the manuscript (e.g., pages 4, 6, 10, etc), which should be corrected.

The reference to equations, figures, tables, sections, and appendices in the text does not follow the WES guidelines, as for the format of the tables.

There are several punctuation and capitalization issues throughout the manuscript. For example, there are unnecessary commas (e.g., line 216), incorrect capitalization where it should not appear (e.g., caption of Fig. 2), and missing capitalization where it should be used (e.g., line 651).

Some words extend beyond the page margins on several lines and should be corrected.

Some parts of the methodology appear in the results section, and conversely, some results are presented in the methodology section.

Detailed comments:
Line 84-85: “ρ [kg m−3] is the air density which is assumed to be constant throughout the swept area of the blade”. The specific value of ρ should be specified here, or a reference to Table 2 should be made.

Line 94: the sentence “we integrate over the rotor-swept area…” should specify which quantity is being integrated. This holds for the caption of Fig. 1, which should be detailed.

Figure 1: a unique notation should be used for the vertical coordinate (z, h, or Z) and should remain the same in the following equations.

Equation 3: Variable N is not defined in the text. It can be specified in the sentence above by adding “at the order N”.

Line 104: “The full derivation is given in A…”. Here, the authors refer to the appendix, but A corresponds to the rotor swept area.

Line 106: “expansion coefficients i, j & k.” Please replace “&” with “and”. Same remark for line 113.

Table 1: this table is present two times in the paper (in the main text and in the appendix). It should be removed from the main text.

Line 114: “recommended at N = 3”. Is there a reason for this specific value?

Line 125: “. It has been shown that a linear scaling factor of 1.81 applied to σv effectively accounts for the heavier tails of the Student-t distribution in the case of the Gotthard Transect Experiment for all wind directions and speeds.” A reference is missing for this statement.

Equation 6: some terms are not explained. Please detail what vin, vout and P(v) are here. Same remark for Eq. 7, where Pr is not defined. In this equation it is not clear whether v refers to v or v . Moreover, the P(v) in Eq. 6 seems to be different from the one in Eq. 4. If this is the case, another notation should be used.

Line 135: “showing good agreement with the analytical solution (Fig. 6b, further detailed in the Results).” This sentence should be in the results section.

Line 178: “When comparing to the measured power output of the turbine (Ptrue), setting the shaft tilt to zero introduces a small bias of approximately 8kW for the 2.35MW turbine.” Here, the discussion refers to a turbine model that is not yet introduced in the paper.

Table 2: how was this specific density value selected?

Line 208: “constant and uniform wind profile with no turbulence, which is detailed in section 3.2.” The reference case is actually defined in the same section, from lines 212 to 215.

Line 211: What is [a)]?

Line 219: “and z = 0m at the nacelle of the turbine”. This sentence should be moved and included in the description of Fig. 1.

Line 232: please correct “Von Kárman” to “von Kármán”. On the same line, how did the authors select the value of z0 = 0.1 m?

Line 239: “indicated orange in Figure 3a”. There is no a) or b) on this figure.

Line 242: “In 2023, the site hosted a Doppler wind LiDAR campaign in which the instrument was deployed at 10 locations near the turbines over a three-month period (Figure 3).” The lidar model and the dates of the field campaign should be briefly indicated.

Line 295: “we have selected a four hour window of 10-minute data”. It is not clear whether the analysis is based on the mean profile over this period or on the 24 individual profiles available.

Line 324: “For the analytical model, we align with the Enercon E92 2.35MW wind turbines installed at the Gotthard Wind Park. Power curve data is taken from the Enercon E92 specification sheet and is fitted (Equation 7), resulting in a smooth analytical expression (Fig. 5a).” These sentences, except the reference to Fig. 5a, describe the methodology and should be moved to the methodology section.

Line 330: The term “power curve” is incorrectly written as “powercurve” several times in the text.

Figure 5: the text indicates that a scaling between the Enercon E92 and the WindPACT turbines is applied to allow comparison of the results. This figure should therefore be plotted using this scaling. Moreover, including additional points on the curve in Fig. 5b (for example, between 9 and 14 m s⁻¹) would result in a smoother curve. The wind speed unit should be written as ms-1 instead of m/s; this should be corrected in the x-axis label.

Line 359: “The OpenFAST model consistently increases with shear…”. I think the word “power” is missing here.

Line 376: the description here refers to Fig. 6c and not Fig. 6b.

Line 376-377: “a characteristic shape which has previously been reported in similar works such as Gasser et al. (2025)”. This reference does not seem relevant here, as no curve (or result) similar to the one presented in Fig. 6c is presented in Gasser et al. (2025).

Line 391: brackets are missing around the references.

Line 392: the authors likely mean Fig. 6d.

Line 395: “from the uniform inflow amounting to only about 15 kW.” This value is right for the analytical model, but the deviation reaches 20 kW in the case of the OpenFAST simulations.

Figure 6: The same remark as above applies here for the x-label unit. As explained before in the text, different values of a, max, and TI are considered, however, the impact of these different values is not discussed. The meaning of these parameters should also be briefly indicated in the caption.

Line 413-414: “Compared to the turbulence-free case (Fig. 7b), this model version achieves much better agreement with the measured power production, particularly at high wind speeds.” This conclusion is not obvious from the figure alone. Although there is indeed a slight improvement when turbulence is included in the model, this only becomes clear when considering the bias values reported in Table 3, since the order of magnitude of the biases is much smaller than the scale of the figure.

Figure 7: the caption does not describe what is shown in the figure. Given that the inclusion of turbulence in the model has a limited impact, it would be interesting to present the power curves obtained with the analytical model and/or OpenFAST in comparison with the one derived from the standard approach. This would confirm the statement in lines 432-433.

Line 423: “the third subfigure (Fig. 7)” corresponds to Fig. 7c.

Table 3: it seems that this table is included in the manuscript as an image. If this is the case, this should be modified, and the table format should follow the WES guidelines.

Line 434-435: it is not clear how the values of 8.6% and 25.4% were obtained. They should therefore be verified.

Line 454: “In Figure 8a, the original LiDAR wind measurements are shown in orange”. One could understand that the authors refer to the measurements from turbine 1 under southerly winds, but this should be stated in the text.

Line 457: “the wake from Turbine 2 intersects the LiDAR beam but consistently bypasses Turbine 1”. Please clarify how this was established.

Line 490: the link between the discussion in this paragraph and the analytical model is not clear. This should be better explained in a revised version of the manuscript.

Line 510: “such as shear, veer”. Please specify linear shear and linear veer.

Equation A4: the lower limit of the summation is missing. The same applies to the remaining summations in the appendix.

Equation A5: this equation is basically the same as Eq. A3 and should not be repeated.

Equation A6: standard functions as sin, cos, and arcsin should be written in normal font rather than italics. The same holds for the differential in the integrals.

Equation A11: it should be specified that the function Q depends on the indices i, j, and k. Qm can then be used in the following equations.

Line 580-585: the demonstration can be simplified by not splitting the integral into two parts, as it can be directly evaluated using the Beta function with x=s+1/2 and y=3/2.

Line 591: it should be specified that the second term is included.

Line 596: another variable should be used since z already corresponds to the vertical coordinate in the main text.

Equations A25 to A27: these equations should not be detailed here since the formula given in Eq. A28 is well known.

Line 634: I recommend introducing a notation for this fraction (e.g., F(m)) and defining it explicitly, since it is currently unclear whether the factor 1/2 is included or not.

Line 649: a detailed calculation of the integral should be provided to confirm that statement. The same applies to section A3 of the appendix.

Equation A9: since the term O(h4) is only used once in the manuscript, I suggest removing it from the equation, replacing “=” with “≈” and specifying “Taylor expansion at the order 2” in the sentence above. Moreover, the choice for the vertical coordinate notation should be consistent in the manuscript (h or z).
Citation: https://doi.org/10.5194/wes-2025-271-RC1
- AC1: 'Reply on RC1', Brandon van Schaik, 15 Apr 2026
  
  We sincerely thank the reviewer for this thorough, constructive, and thoughtfully written review. We greatly appreciate the positive and encouraging tone throughout, as well as the clear and detailed feedback provided. The comments are insightful and have helped us to better structure and clarify the manuscript, improving both its readability and scientific rigor. We are grateful for the time and care invested in this outstanding review and have addressed all points in the document attached.
  
  Citation: https://doi.org/10.5194/wes-2025-271-AC1
RC2:
'Comment on wes-2025-271', Anonymous Referee #2, 03 Apr 2026

Paper presents a new method for estimating wind measurements, improving on single point measurements, for use in power curve assessments. The paper is well written and provides clear explanation of methods and experimental setup. The proposed methods are demonstrated in a clear way in studies using collected field data. All in all a well-written paper and a good contribution.
General comments:
Good that the paper makes frequent comparison to the standard approach in EIC 61400. Is there an intention to submit this work for consideration to a future standard?
Specific comments:
Page 2 Line 50: "These discrepancies scale to wind-farm level and can lead to significant instantaneous and cumulative power prediction errors" -- This depends a little if the error per-turbine is biased in one direction, it could also cancel out.
Page 3 Line 65: "developed by NREL" (could note now NLR per name change)
Page 3 Line 69: "2106m a.m.s.l." please define
Page 3 line 70: "while modelling a virtual wind turbine with open-source blade geometry", do you mean modeling the Enercon E92s as this turbine, or seperately modeling this turbine?
Page 4: "where horizontal variations across the rotor disk are usually minor compared to the strong vertical gradient in wind speed." -- perhaps unless wakes are present?
Page 7: "given arrays of measured wind speeds v and heights z, t", are the wind speeds v instantaneous or averaged measurements?
Page 7: "We refer the reader to the Data Availability section of this manuscript for more details." Thank you for this contribution to open-source and data availability.
Page 8: Equation 7, I think a figure comparing the data-based, or binned power curve against the functional approximation would be helpful to see. Does the equation have a range of wind speeds for which it is valid or does it work cut-in to cut-out?
Page 8: "it naturally enables the removal of anomalous or clearly unphysical measurements before constructing the analytical profile", a more standard approach might be to only include data from wind sectors where the turbine is not waked right?
Page 11: "resulting in 25 simulations per power curve." how many power curves in total? A standard approach might include 4-6 random seeds per wind speed but that could be unnecessary here and I'm not saying you should do it. Just noting.
Page 21: Line 387: , "so the controller cannot hold the blades exactly at the optimum." Since this is above rated operation, the controller would not be trying to keep the blade at optimum but instead be pitching toward feather to keep the turbine from exceeding rated power. If the torque controller is a simplified constant power (versus constant torque) operation at and above rated speed, then the explanation is more probably that the variations induce rotor speed excursions above and below the rated speed, but the power is clipped above but still falls below, leading to a downward bias.
Still I'm a little surprised these above rated power deviations can be on par with the deviations happening near rated. If you take a look at a standard power curve adjustment for TI you often see the pattern you see with an increase in power away from rated, a decrease near and slightly above rated (like a rounding of a sharp corner) and then minimal effect above rated. There could also be a bug in the controller.
page 25: "OpenFAST generates power earlier because it lacks a defined cut-in wind speed – a known unrealistic feature of the software", this could be defined in the controller. But it's not a major point worth the effort to fix.

Citation: https://doi.org/10.5194/wes-2025-271-RC2
- AC2: 'Reply on RC2', Brandon van Schaik, 15 Apr 2026
  
  We thank the reviewer for the constructive feedback that has helped to improve the structure of the manuscript. We have provided our comments in the document attached.
  
  Citation: https://doi.org/10.5194/wes-2025-271-AC2

Peer review completion

AR – Author's response | RR – Referee report | ED – Editor decision | EF – Editorial file upload

AR by Brandon van Schaik on behalf of the Authors (15 Apr 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (26 Apr 2026) by Etienne Cheynet

RR by Anonymous Referee #2 (29 Apr 2026)

RR by Anonymous Referee #1 (21 May 2026)

Suggestions for revision or reasons for rejection

General remarks

Major remarks
We are disappointed that our remarks on the previous version of the article have not been taken into account, contrary to what the “answer to reviewer” document says. Some section titles have been changed, and some content has been moved, but the order in which the paper flows is still the same, meaning the methodology section remains messy and difficult to follow. In particular, the OpenFAST configuration is still split between two sections (2.2 and 2.4.2), and the power curve retrieval and analysis is split between three sections (end of 2.1.2, 2.1.3, and 2.2.3).
We can understand that, given the report produced by the second reviewer (that says the paper is clear), a choice was made to make minimal corrections and keep the article structure unchanged. However, we also requested more explanation about the way turbulence is taken into account in the analytical model, which were not provided by the authors. In particular, the article text does not allow relating the theory to the numerical implementation, i.e., the outputs of the boxes in the block diagram (Fig. 6) do not match the mathematical notations introduced in Sec. 2.1.
Firstly, the output from the “Power curve fitter” box on Fig. 6 is the power coefficient Cp, so that Sec. 2.1.2 should explain how Cp is determined after the Ppc(v) curve fitting (or a reference provided). Secondly, the outputs of the “Taylor expansion” box on Fig. 6 are two variables called cv and cσ_v that are not defined in Sec. 2.1. My guess is that they are the Taylor coefficients resulting from the expansion of the wind profile (cv), but also of the expansion of the wind standard deviation profile (cσ_v), but no explanations are given about this second Taylor expansion anywhere. Sec. 2.1.2 must absolutely explain how the dependency of wind standard deviation upon altitude is taken into account in the analytical model (see also detailed comments about Eq. 7 and 8). Similarly, the idealized wind profiles (Sec. 2.3) are not associated with an idealized turbulence profile, so it is not known if turbulence was included or neglected in these test cases (see also detailed comments about this section).
At this stage, readers wanting to implement the method proposed in this paper using another programming language would need to do some reverse-engineering of the code provided on Zenodo to really understand what was done. The point of an article is to allow the reproducibility of the work (not just running the code provided by the authors, but really understanding what it does), and this paper does not provide sufficient explanations to fulfill this purpose, no matter what the other reviewer said about its clarity.
Therefore, our recommendation is again “major revision”, hoping that our remarks will be understood and properly answered this time.

Minor remarks
We do not agree with the removal of units in the text when referring to the numerical value of physical quantities, even if these quantities have been previously defined. For instance (line 435), writing “the sudden drop of the OpenFAST curve at v = 12.” instead of “v = 12 m s−1.” makes no sense. Following this logic, why not suppress the degree symbol after the shear angle values (lines 451-452)? Also, the m s−1 unit is still present in other sentences (line 498), so this unit-removal policy has not even been applied everywhere.
We agree that square brackets can be used to give the associated unit when defining the notation of a physical quantity, but brackets should not be used when giving numerical values. There are still some left in the text (e.g., with the surface roughness line 315 and in the legend of Fig. 7). Also, some units are still in italics (line 498) and should be turned into regular font. Other small points mentioned in the previous review have not been corrected (see for instance detailed comment about lines 315 or 457).
Thorough work is still needed on the reference list to stick with WES guidelines, i.e., provide the DOI for all publications that have one and use journal name abbreviations. The latter can be found for instance here: https://woodward.library.ubc.ca/woodward/research-help/journal-abbreviations/. Also, many references are incomplete in the sense that the type of document is not identifiable (see detailed comments for examples).

Detailed remarks

Introduction
Line 55 (Eq. 1). The notations Ai and A must be defined.
Line 75. Minus sign differs from a simple dash and must be coded as $-$ in Latex.
Lines 100-105. Detailed information about the study site (altitude) should be given in Section 2. Same for detailed information about the lidar observations (e.g., vertical/time resolution). In the introduction, you can just say it is a mountainous site with complex terrain where wind profiles were measured using lidar during a field campaign.
Line 101. The acronym SCADA is not defined.
Line 109. The introduction is supposed to end with an announcement of the article’s plan.

Section 2.1
Line 111. “Equation 2” should be abbreviated “Eq. 2” as it is in the text. The word Equation should be used only when it appears at the beginning of a sentence. The same holds for sections, figures, and so on, as mentioned in the WES guidelines. This was already said in the remarks on the previous version of the article, it should be good to take it into account and correct it throughout the manuscript.
Line 112 (Eq. 2). There should not be a dependency upon z in P and v in this formula, because as you indicate, the wind speed is an equivalent wind speed over the rotor-swept area. It would be clearer to remove the z dependency and replace v with veq (which can be the Ueq from Eq. 1 or the new formulation you are about to introduce).
Lines 119 and 121. There are two redundant sentences here: “vertical variations across the rotor-swept area are usually the dominant factor, often far exceeding horizontal deviations” and “horizontal variations across the rotor disk are usually minor compared to the strong vertical gradient in wind speed,”
Figure 1. There is a h remaining on the side of the triangle, please replace it with z for consistency.
Line 130. “Where R[m] is the radius of the rotor-swept area of the turbine,”. Here, you specify the unit for R, as if you introduce the unit of a new notation. However, R was already used on line 115 and its unit was not defined here.
Equation 5. To what speed exactly does the v dependency of P and Cp refer? Is it the equivalent wind speed in the rotor swept area, which is actually the cubic root of the summation term in the formula? If so, it should be said, and a more explicit notation than v should be used in Eq. 5. If otherwise, please explain.
Lines 157-158. “(recommended at N = 3 providing a good trade-off between capturing essential behaviour and avoiding over-fitting)”. This has already been said above and should be removed here.
Line 164. “We refer the reader to the Data Availability Section of this manuscript for more details.” There is no “Data Availability” section, but rather “Code and data availability”. Moreover, this section should appear after the Appendix.
Lines 167 and 171. “Student-t distribution” the dash is at the wrong place: “Student t-distribution”.
Equation 7. It is not clear if this wind speed distribution applies to the equivalent wind speed in the rotor-swept area or to the wind at each altitude of the profile. In the first case, the notation v bar actually corresponds to the cubic root of the summation term in Eq. 5, which should be said (and a more explicit notation such as Veq should be used). And then, you need to explain how the variable σv in Eq. 7 is computed from the profile of wind speed variances using, I guess, the Taylor expansion of this profile. In the second case, you need to explain how the wind speed distribution at each altitude is related to the wind speed used as an integration variable in Eq. 8. These explanations are mandatory to add because their absence makes it impossible to understand the processing of turbulence in your analytical method.
Lines 181-191. Explanations about the power curve model should be moved to Sec. 2.1.3. As said in the major comments, Sec. 2.1.2 must explain instead how the dependency of wind standard deviation with altitude is taken into account.
Lines 193-194. “The analytical formulation of Equation 9 is fitted to the published power curve of the Enercon E92 2.35 MW wind turbine using manufacturer data from the technical specifications.“ A reference is missing here.
Lines 195-196. It should be specified which parameters are fixed following the turbine technical specifications (likely vin, Pr, and vout) and which parameters are actually fitted (B and C).
Figure 2. The legend is wrong “Fit (Eq. 7)” should be corrected as “Fit (Eq. 9)”.
Sec. 2.2.2. Please avoid one-sentence paragraphs.
Line 249. “from 1 to 25” missing wind speed unit.
Lines 255-256. “Remaining with Figure 3, the OpenFAST simulations cannot be based on the Enercon E92 directly, as the required blade geometry to simulate power production is proprietary. Instead, the open-source WindPACT 3.0 MW turbine is used.” All this has already been said, please do not repeat.
Figure 3a. Here, Cp is called coefficient of performance, while it was defined as power coefficient at the beginning of Sec. 2. Pointing it is the same thing somewhere might be good.

Section 2.3
Equations 10 to 12. If we follow Eq. 10, then ΔPshear,an should simply be noted ΔPshear, precising that Pref corresponds to the uniform profile. Please be consistent with your mathematical notations.
Lines 302-303. “−R and R and the bottom and top of the swept area of the blade”. This has already been defined at the beginning of Sec. 2. The point of defining unequivocal mathematical notations is to be able to use them throughout the paper without having to re-explain them each time they appear. While we are talking about notations, v bar usually denotes the speed average from Reynolds averaging, so that vhub or v0 would be a better choice to denote the wind speed at hub height.
Lines 309-312. What is the wind profile associated with the homogeneous TI? And conversely, what is the profile of TI associated with the other idealized wind profiles? It seems to us that for each idealized profile, both the wind and the TI profile should be defined. If you assume the absence of turbulence in the uniform, linear shear/veer and logarithmic profiles, it should be said.
Line 315. “Von Kármán” should be corrected to “von Kármán” with a lowercase v, as already indicated in the previous review.
Lines 318-321. A three-line section is not relevant. Either you need this section to explain the metrics used to assess the model performances, or you can merge 2.3.1 and 2.3.2.

Section 2.4
Lines 329-330. “This wind farm is situated 2106 m a.m.s.l., north–south-oriented Gotthard Pass in the central Swiss Alps.” Some words are missing, please correct.
Equation 13. It would be better to replace the constants 50/46 and 12.478 with appropriate notation and define their values in the text. This would help readers to adapt the method to other sites/turbines with different altitudes/sizes.

Section 3.1
The discussion has significantly improved in this section, notably by making better connections with the analytical formulas.
Lines 455-457. “The ∆P curves of homogeneous turbulence, shown in Figure 7c, has a characteristic shape which has previously been described to follow this relationship between power curve curvature and power contributions related to turbulence in similar works such as ?” This sentence is awkward. Maybe: “The ∆P curves of homogeneous turbulence, shown in Figure 7c, have a characteristic shape: such a relationship between power curve curvature and power contributions related to turbulence has been previously described by [reference].”
Line 457. The missing reference signalled in previous version of the paper is still missing here.

Section 3.2
Lines 522-523. As previously mentioned in the first review, the percentages provided here are incorrect. Even if you specified the formula in the new version of the article, it is not clear how you obtained a minimum bias reduction of 8.6 % and a mean of 25.4 % (should be 7.8 % and 27.2 % instead). Please correct the values accordingly (in the abstract and conclusion as well).

Section 3.4
Line 579. “the simpler configuration which are comparable” should be “which is”.

References
Line 771, Albers. If this is a book, a publisher should be indicated.
Line 772, Antoniou et al. The web link points to a presentation, if this was shown at a conference/workshop, the name of the gathering should be provided.
Line 774-775, Belu et al. We are unable to say what type of document this is. Was it a conference proceedings, a journal article, or something else? A web search only points to a PDF document available on ResearchGate, which cannot be considered an official repository.
Line 776, Bot. This one is a report, with a report number, so it should be cited as “ECN report number XXX” or something alike rather than simply “ECN”. Also, it is available online (https://publications.tno.nl/publication/34629395/v931oD/e16041.pdf), so the link could be provided.
Lines 777-779, Brown et al. Journal abbreviation should be used, missing page number, and missing DOI.
Line 780-781, Choukulkar. Journal abbreviation should be used, missing DOI.
Line 786, Emeis. This one is from the Deutsches Wind Energie Institut magazine, so it should be cited as it, with the issue number.
And so on… we are not going to go through the full list, but all references should be carefully checked to ensure they comply with the WES guidelines and make the type of document clearly identifiable.

Typos:
Some section titles (and the article title itself) have capital letters at the beginning of every word, but only the first word should be capitalized.
Line 559. The minus sign should be coded in LaTeX math mode (looking like a long dash instead of a short dash).

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ED: Reconsider after major revisions (27 May 2026) by Etienne Cheynet

AR by Brandon van Schaik on behalf of the Authors (09 Jun 2026) Author's response Author's tracked changes Manuscript

ED: Referee Nomination & Report Request started (15 Jun 2026) by Etienne Cheynet

RR by Anonymous Referee #1 (20 Jul 2026)

Suggestions for revision or reasons for rejection

General comments

We are pleased to see that the remarks we made about the organization of the manuscript and the necessary explanations of all the aspects of the method have now been addressed. Most of the comments on this version are minor ones. The scientific points that still deserve an answer concern the computation of the turbulence integral length scales and the comments about these results (see detailed comments on Sec. 4.4 and App. B).

Detailed comments

Section 1. Introduction
Lines 98-100. “The contribution of the study…”: in this sentence, it would be better to remain more general, i.e. not mention OpenFAST and the Gothard Pass site, that have not yet been introduced, but rather numerical simulations and a mountainous site. The transition to the next sentence would remain natural.
Lines 101-104 and 105-107. As already said in the previous review, one-sentence paragraphs should be avoided.
Lines 112-114. “The results then compare…”: a reference to Sec. 4 should be added in this sentence.

Section 2. Background and theoretical framework
In our opinion, it would be more logical to present the two paragraphs of Sec. 2.2 in the reverse order. Also, subsections 2.1 and 2.2 could be merged: it is possible to introduce the rotor power very short subsections should be avoided).
Line 147. It is incorrect to say that “the instantaneous wind speed at height z” is given by Eq. 3. Actually, it gives the probability density function that models the distribution of instantaneous wind speed values at height z.
Line 182. Since this is the first time the authors mention an appendix in the text, it should be Appendix A instead of B, and the order of appearance should be reversed in the Appendix section.

Section 3. Methodology
Lines 184-197. Instead of using (i), (ii), etc., it would be clearer to refer to the actual subsection numbers.
Line 198. Same remark: point to the actual subsection number instead of a vague “below”.
Line 208 / Eq. 8. What does U denote here? Is it the hub-height wind speed or the equivalent wind speed? We get it that it comes from the turbine technical specifications, but it would be good to precise what it is.
Line 212. The website url should be included into a reference and not directly in the text.
Lines 223-224. “the mean wind-speed profile and the wind-speed standard-deviation profile are both represented [by a Taylor expansion] over the rotor layer. The words within [...] are missing for the sentence to actually bring some information. A colon is also missing at the end of line 224.
Line 226. Writing about the Taylor coefficient for the mean wind while the formula just above does not use them is confusing. It would probably be clearer to say that the the wind-speed standard-deviation profile is represented by a Taylor expansion in a similar way to the the mean wind-speed profile, using coefficient noted as c_{sigma_v,i} instead of c_{v,i}.
Lines 229 and 231 / Eq. 11 and 12. Are the <P_z> numerical values or analytical expressions? If they are numerical, then P_turb is a discretized integral and the z step should be precised.
Section 3.4 was better in the previous version, i.e. the cases description and formulas that have been moved to Section 4.1 should have stayed here. We understand that the authors wanted to give only the methodological framework in Sec. 3, and show the application cases in Sec. 4. However, for readability, it is better to give all the analytical formulas in the methodology section, so that Sec. 4.1 can focus on the results in terms of power.
Line 261. “cross-streamwise” is just “cross-stream”
Line 268. “its influence on the results is presented” -> “will be”
Line 269. “As shown later in Sec. 4.4, and relevant for the methodological choices made here,” this makes an awkward transition from the previous sentence ending by “Sec. 4.4”. Consider replacing by something more simple like “In particular, it will be shown that…”
Line 281-282. “the inflow advects over several kilometres”: this sentence is awkward. The verb “to advect” should be used in passive form, e.g. “the air mass is advected over several kilometres”.
Lines 292-293. The numerical values are given in Table 1 so there is no need to remind them here, nor give the numerical formula (Eq. 17). You can just say that h_E92 and h_WP3.0 are the hub heights and R_E92 and R_WP3.0 are the rotor diameters of the E92 and WP3.0 turbines, respectively, which values can be found in Table 1.
Figure 5. Please carefully check that the scheme is consistent with the formulas in the text and that all relevant parameters are mentioned. As for now, there are still small mismatches between the math notations above the arrows and the text: for the power curve fitter, v should be U and P(v) should be P_cp(U); for the wind profile scaling, the r should be R; for the outputs, P_AN should be P_an. Some of the parameters, like ∆z_lidar or v_in / v_out, do not appear on the scheme so far.
Lines 307-310. A reference to Sec. 4.3 should be added in this paragraph.

Section 4. Results and discussion
Line 721. There must be a space to remove between the parenthesis and the dot.
Table 2. The minus sign differs from the dash symbol, please use a proper minus sign for the negative values (to pick up in the special characters in Word).
Lines 529-530. “the individual 10-minute estimates show large variability, ranging from a few metres to several hundred metres depending on height, component, and inflow period”: this statement should be supported by (a) figure(s) (see the comment about App. B, line 759) as Table B1 does not give a full picture of the length scale variability.
Lines 541-543. “The tested configurations include the original short-scale USRVKM example profile, a modified component scaling of (1.0,0.8,0.6), a length-scale profile increased by a factor of ten, and a combined case in which both modifications are applied.” So the length scales derived from the lidar observations were not used for the simulations? A comment would be needed, saying for instance that these values are covered by the ×10 case.
Lines 546-547. “from 1151 kW in the base case to 1151 kW for the modified component scaling, 1151 kW for the increased length scales, and 1150 kW when both modifications are applied.” As the values are all the same (or almost), they are not useful. The results should be directly given in terms of difference to the base case, only reminding the base case power value at the end of the paragraph.
Lines 551-552. “This was done for the representative case in which the largest deviations in the velocity spectra were observed”: does this sentence only refer to the seed test or to all the turbulence sensitivity tests? If it is the latter case, then this information should be provided earlier, around line 541.
Line 552. “corresponding to wind profiles around 9 m/s” -> “speeds”, not “profiles”.

Appendix B
The references relative to the method described in this appendix must absolutely be provided.
The notations must be clarified, as the text oscillates between the zonal/meridional and the streamwise/cross-stream decomposition of the wind.
Lines 741-742. “the five beam azimuths” rather than “positions”. Also, “V” should be vertical, please avoid jargon.
Lines 743-744. The way you explain it, u and v do not appear to be the streamwise and a so-called “lateral” wind component, but the meridional and zonal wind components (and by the way, the usual notation are the reverse). If you did compute the streamwise and cross-stream components, it should be said more clearly. The formula do not need to be reminded, as this decomposition is common, but a reference should be provided.
Line 744. The “V” can be removed after “vertical beam”.
Line 749. The index i is not u, v or w, as we actually have u_1=u and not u_u, u_2=v and not u_v and u_3=w and not u_w. It would probably be easier to directly introduce the u_i’s in the previous paragraph.
Line 752 / Eq. B3. The autocovariance function computed from the radial wind speeds recorded in a single beam direction is impacted by the lidar instrumental noise at zero lag (Bonin et al., 2016; Lenschow et al., 2000). In this case, the autocovariance function must be extrapolated towards the zero lag instead of using the zero-lag value as it is. How is this point dealt with when computing autocovariance after combining several beams? Did you perform any kind of instrumental noise correction?
Line 758 / Eq. B5. This equation suggests that u an v are the streamwise and cross-stream components of the wind, which is in contradiction with lines 742-743. Please clarify.
Line 759. If we understand correctly, turbulence length scales derived for all the lidar positions within the Gotthard Pass, for all inflow directions and for all hours of the day have been used altogether to compute the median and percentiles. Did you investigate if the observed variability in length scales could be related to the lidar positions, the main inflow directions, or the night/day contrast? We would like to see figures allowing to see the variability and distinguish the different sites, inflow directions and hour of the day, for the streamwise length scale and the scaling factors, though this could be put in supplementary.
Lines 759-760. “uncertainty margins are calculated from the 16th–84th percentile range”, why was this peculiar percentile interval chosen?
Line 766. The notation α already refers to the veer angle. Using another letter would be clearer.

Typo
The font used for indices in math notations should be italic when it refers to a variable (c_v, K_m…) but regular when it is a precision in the variable name (P_an, v_in…).
Some references to equations still do not follow the WES guidelines (eg., “Eq.2” in line 126 that should written as “Equation 2”). The same holds for appendices, that should not be abbreviated (line 182 and further in the text).

Reference list
For conferences, “International Conference” is usually abbreviated as “Int. Conf.”, then you should try to build an abbreviated conference name based on similar journal names, for which you can check the normalized abbreviations e.g. from:
https://woodward.library.ubc.ca/woodward/research-help/journal-abbreviations/
Letizia et al.: “Journal of Physics: Conference Series” should be abbreviated as “J. Phys.: Conf. Ser.” as for Clifton et al. or Niayifar et al.
Murphy et al. et Troldborg et al.: “WES” is not the proper abbreviation for Wind Energy Science, but “Wind Energy Sci.”
Redfern et al.: “Monthly Weather Review “ should be abbreviated as “Mon. Weather Rev.”
Stull: the title “An Introduction to Boundary Layer Meteorology” is repeated at the end of the reference, please correct.

References cited in this review
Bonin, T. A., Newman, J. F., Klein, P. M., Chilson, P. B., and Wharton, S.: Improvement of vertical velocity statistics measured by a Doppler lidar through comparison with sonic anemometer observations, Atmospheric Measurement Techniques, 9, 5833–5852, https://doi.org/10.5194/amt-9-5833-2016, 2016.
Lenschow, D. H., Wulfmeyer, V., and Senff, C.: Measuring Second- through Fourth-Order Moments in Noisy Data, J. Atmos. Oceanic Technol., 17, 1330–1347, https://doi.org/10.1175/1520-0426(2000)017%3C1330:MSTFOM%3E2.0.CO;2, 2000.

Referee Report: PDF

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ED: Publish subject to minor revisions (review by editor) (27 Jul 2026) by Etienne Cheynet

Dear Brandon van Schaik and co-authors,

Thank you for revising the manuscript. I have now received the report from the remaining reviewer, who recommends a minor revision. I am therefore pleased to recommend a minor revision, with the revised manuscript and point-by-point response to be assessed by the editor (me). Please carefully address all the reviewer’s comments in your response.

Regarding the treatment of turbulent integral length scales, I recommend removing this discussion, including the associated analysis in Appendix B and Section 4.4.The baseline profile L=[3,4,6,9,13,13,13] m is taken from the TurbSim USRVKM example file. That file explicitly states that these values are completely arbitrary and should not be used in simulations. They therefore cannot provide a scientifically defensible baseline, even for a sensitivity analysis. Demonstrating limited sensitivity to modifications of an arbitrary baseline does not validate the baseline itself.

The LiDAR-derived estimates of the integral length scale seems too unreliable to be useful, unfortunately. The estimated streamwise integral length scales have medians of approximately 50–70 m but spreads of approximately 70–100 m. Moreover, the inferred scaling (L_w/L_u=1.20), implying a vertical-velocity integral length scale larger than the streamwise-velocity integral length scale, is not physical. Thus these data do not appear sufficiently robust to define component-specific integral length scales for TurbSim.

More importantly, the manuscript shows that the precise turbulence-spectrum and length-scale settings is not absolutely needed for the conclusions of the manuscript. I therefore suggest keeping the turbulence sensitivity analysis simple: A deterministic case without turbulence may be compared with a turbulent case based on the IEC Kaimal Normal Turbulence Model, using an appropriate representative turbulence intensity. There is no clear need to use the user-defined von Kármán spectrum or to prescribe site-specific integral length scales. Removing this secondary discussion would shorten the manuscript, improve its clarity, and avoid unsupported physical interpretations that are not necessary for the main conclusions.

Best regards,

Etienne Cheynet

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AR by Brandon van Schaik on behalf of the Authors (21 Aug 2026) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (27 Aug 2026) by Etienne Cheynet

Dear van Schaik et al,

Thank you for the substantial work undertaken in revising the manuscript. The paper has made good progress; however, a few remaining issues need to be resolved before it can be accepted.

Lines 172-174 and 267-268:
The terminology concerning turbulence in TurbSim should be corrected. The turbulence spectrum prescribed in TurbSim is not itself stochastic; it defines the target spectral density. The stochastic character of the generated time series arises from the random phases used to construct the turbulent realization. I therefore suggest avoiding the expression "stochastic turbulence spectrum".

A shorter and more accurate formulation would be:
"TurbSim is used to generate the turbulent inflow fields required by OpenFAST."

Lines 175-180 and 274-276:
I do not object to the use of USRVKM or to the use of height-dependent turbulence parameters. However, the integral length scales supplied to USRVKM must be physically realistic.

The values used in the TurbSim example file cited by the authors are explicitly described in the TurbSim documentation as made-up demonstration values and should not be used as an atmospheric parameterization. The values used here, approximately 3-13 m, are also substantially smaller than realistic atmospheric integral length scales. This is not merely a matter of interpretation. The integral length scale is an input to the von Karman spectrum and directly controls the distribution of turbulent energy across frequencies. Using unrealistically small integral length scales shifts the spectral peak towards substantially higher frequencies and therefore produces an unrealistic turbulence spectrum.

Consequently, stating that "the prescribed length-scale values are treated only as numerical inputs" does not resolve the problem. The integral length scale is indeed a model input, but it is a physical model parameter with a direct effect on the generated turbulence field. Whether or not the authors assign physical meaning to it in the discussion does not remove its physical effect on the simulation.

I therefore request that the authors replace the arbitrary TurbSim example values with a physically defensible height-dependent integral-length-scale profile and rerun the affected turbulent simulations. A straightforward option would be to use a standard-based atmospheric length-scale formulation, for example the expression given in Eurocode EN 1991-1-4:2005+A1, Annex B, Eq. B.1, or another published formulation appropriate for a von Karman spectrum. The selected formulation and its applicability should be stated clearly.

This would be a considerably simpler and more defensible solution than retaining known unrealistic values and adding extensive discussion to justify their use.

Best regards,

Etienne Cheynet

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AR by Brandon van Schaik on behalf of the Authors (21 Oct 2026) Author's response Author's tracked changes Manuscript

ED: Publish subject to minor revisions (review by editor) (23 Oct 2026) by Etienne Cheynet

Dear authors,

Thank you for the revised manuscript. After a final review, I identified a few remaining inconsistencies that I would like you to address before publication.

- Page 11, lines 224-232: Equation (12) currently has units of power multiplied by area. It appears that a factor 1/A is missing. Otherwise, the dimensions are inconsistent. Furthermore, if Equation (13) is intended to represent the contribution of turbulence alone, I would expect it to approach zero as the turbulence intensity tends to zero. Please verify that this is indeed the case, including for a nonuniform mean wind profile, and check the consistency between Equations (11)-(13).

- Eurocode turbulence length scales: The revised formulation appears correct, but the manuscript does not specify the value of z_0 (roughness length) used in the simulations. This should be documented for reproducibility. Was z_0 = 0.1 m used, as in Fig. 6?

- Page 35, Appendix A3, lines 655-661: Shouldn't the coefficient c_2 have a negative sign? There appears to be a minor algebraic error in the derivation.

- Equation (A12): Please check the dimensional consistency. Since alpha_max is an angle (expressed in radians), the term containing alpha_max^2/R^2 is not dimensionless. Should R^2 be omitted from the final expression?

- Page 25, lines 430-434: The expression "(Analytical - IEC)/IEC" should be presented using proper mathematical notation, with clearly defined quantities. Please also verify the sign convention, as the reported positive bias reductions appear to be based on the absolute values of the biases.

- IEC reference approach: This is an issue I have raised several times during the review process. The manuscript repeatedly describes the reference method as "the IEC-standard approach", based on a single wind-speed measurement. This is potentially misleading, since IEC 61400-12-1:2022 already includes procedures involving rotor-equivalent wind speed and the treatment of wind shear, veer, and turbulence. I strongly recommend using the term "the hub-height-based reference approach" instead of "the IEC-standard approach" throughout the manuscript, where this accurately describes the method used for comparison.

- Abstract: The statement "This equates to an annual energy production estimate that is 5.2 +/- 3.9% closer to reality" is an overstatement. The observational dataset covers only a limited number of selected wind events, which is insufficient to establish an improvement in annual energy production estimates. The statement should be restricted to the improved power or energy estimates for the investigated events.

- Polynomial order: Section 3.6 specifies a third-order polynomial fit. However, page 27 states that the method can also be applied when only two measurement levels are available. Please clarify that a lower polynomial order would be required in such cases.

- Computational speed: The abstract claims that the analytical model is at least 1,000 times faster than OpenFAST. Without a documented computational benchmark, this quantitative statement is insufficiently supported. I suggest removing the numerical speedup claim rather than introducing additional benchmarking at this stage.

Overall, I appreciate the efforts made to address the previous comments, particularly the revision of the turbulence length-scale formulation. I consider the manuscript suitable for publication once these inconsistencies have been addressed. I do not expect additional numerical experiments, provided that the corrections to the equations do not affect the reported results.

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AR by Brandon van Schaik on behalf of the Authors (23 Oct 2026) Author's response Author's tracked changes Manuscript

ED: Publish as is (23 Oct 2026) by Etienne Cheynet

ED: Publish as is (23 Oct 2026) by Julia Gottschall (Chief editor)

AR by Brandon van Schaik on behalf of the Authors (23 Oct 2026) Manuscript

Short summary

We created a new way to estimate how much energy a wind turbine can produce by using the full change in wind with height instead of a single measurement. Testing it on turbines in the Swiss Alps showed that it predicts energy production more accurately and smoothly than current industry methods. It performs as well as advanced models but is much faster, helping guide future wind projects in complex landscapes.