Review of ‘A numerical study of the influence of terrain on wakes, blockage, wind farm efficiency, and turbine efficiency’

The article investigates the effect of an idealized terrain on the wake, blockage, and efficiency of wind farms. As articulated by the author, the study aims to extend the existing knowledge on terrain effects on individual wind turbine wakes and efficiency to a wind farm scale. This is a very interesting and important step forward in understanding the effect of terrain-induced pressure gradient on the wind farm performance and flow. Overall, the article is well written and easy to follow. I will recommend publication of the article, given the following questions/comments are adequately addressed:

1. Terrain affects the flow in two ways: by imposing pressure gradients (which then lead to flow acceleration/deceleration) and by changing vertical flow shear – which alters turbulence production in the flow. The first of these effects is thoroughly discussed in the article; however, the second one appears to be completely ignored. It is suggested to at least discuss why terrain-induced turbulence can be ignored/does not play a significant role in this study. In addition, the effect of terrain-induced turbulence is also missing from the discussions/limitations section. I think this effect is worth discussing as well.
2. The simulations use a spanwise inter-turbine spacing of 2D, which sounds very small. It is recommended to add an explanation or justification for choosing such a small spacing. On a similar note, the streamwise spacing in two row wind farm is chosen to be 15D. A possible explanation behind this choice will be beneficial.
3. Given the large number of simulations, I would suggest adding a table summarizing the distinguishing features of different simulations. I see that some selected simulations are summarized in a table in section 3.2. Perhaps a complete description earlier in the study could be added.
4. A brief description/quantification of the free-stream flow in terms of speed-up and turbulence levels will benefit the reader in understanding the flow conditions wind farm/turbines are exposed to.
5. In figure 7, it will be interesting to point the position of turbine rows to give the reader an idea of the pressure gradient experienced by the turbines in different rows.
6. The discussion in lines 289-294 on the effect of wake trajectory is very qualitative. Perhaps a more quantitative approach could be used to support the argument that the trajectory effect is negligible in the current study.
7. A lot of the contours are shown at the ‘hub height’. How is the hub height defined? Is it a local one, meaning at each x, whatever the hub height would be, thereby a terrain-following hub height? Also, as mentioned by the author, and seen in previous studies, the wake trajectory may not fully follow the hub height trajectory. How would that influence the interpretation of some of the results?
8. More details on the assessment for the real wind farm are needed. Specifically, the discussion in lines 620-630 needs to be expanded. For instance, which turbines were chosen for assessment, and what were the criteria for this assessment? Also, it seems that for these turbines, only individual power coefficient changes were assessed. Is this because the turbines were randomly apart from each other?

Comments on wes-2025-291

This paper presents a large set of RANS simulations of atmospheric flow over one or two rows of onshore wind turbines (actuator disks) located in parallel to a quasi-two-dimensional terrain feature (hill or valley). To identify the terrain effects on both turbine-scale and farm-scale efficiencies of power generation, additional simulations for the same turbines on flat terrain are also presented. The simulation method has been validated in the author’s previous publications and no further validation is given in this paper. Overall, these simulations have been designed carefully and the results are very informative, although there are a few points on which the author’s discussion seems insufficient or unclear. I would therefore suggest that the paper be revised considering the following points, before it is accepted for publication.

1. A better explanation and discussion on the mechanisms of (turbine-scale) wake recovery should be given. This is a general comment not only on this paper but also on several other papers in the literature, but I am concerned that the effects of “terrain” and “pressure gradient” seem to have been discussed almost interchangeably. In general, these effects should not be discussed interchangeably, because “pressure gradient” is only one of several things that could be induced by “terrain”. More specifically, the recovery of turbine wakes (or any wakes) should be discussed based on the conservation of both “mass” and “momentum”, and the effect of “pressure gradient” is only part of momentum conservation (as can be seen from the RANS equations). I think the author’s explanation given in the current manuscript would be sufficient if the flow was inviscid, where the acceleration/deceleration of the flow (caused by contraction/expansion of the flow passage due to terrain) would be directly linked to favourable/adverse pressure gradients. But in the real world, where the flow is viscous, this relationship is altered by mixing (or the Reynolds stress due to turbulence). This point needs to be discussed more carefully.
2. Somewhat related to the above point, I think the author’s definition of “blockage” (Lines 64 to 68) is a little unclear. Here the author states that these terms “refer to the inviscid response of the flow to the obstruction” but I think this “inviscid response” may need to be either rephrased or expanded. My main questions are: (1) Why does this need to be specifically about “inviscid” response? (2) Do we really need to define “blockage” in this way, which seems different from its traditional definition of “blockage” in aerodynamics? I understand that the blockage-related terms have been used in different ways (especially over the last 10 years since the concept of “wind farm blockage” was introduced by the author and other people) and I appreciate that here the author is trying to define how these terms are used in this paper specifically, but traditionally, people who work on turbine aerodynamics (especially those who test a turbine in a wind tunnel) tend to consider “blockage” as the ratio of the turbine’s rotor swept area to the cross-sectional area of the flow passage (e.g. wind tunnel). From their point of view, the “blockage” is zero when the flow passage is not constrained laterally, but the turbine still decelerates the flow through its rotor swept area (i.e. “induction” is non-zero even when “blockage” is zero). The author’s definition of “blockage” seems to contradict this traditional view, so this point needs to be explained more carefully.
3. Related to the above point, I think the author’s definition of “induction” (Lines 68 to 69) may also need some modifications. Here the author states that the induction is “the turbine-blockage-related wind speed reduction upstream of the turbine” but I think “turbine-blockage-related” can be confusing (especially to turbine aerodynamicists, for the reason described above). To avoid this confusion, I think it would be better to say that the induction is “wind speed reduction induced by the thrust force of a turbine (or turbines)”. Also, it would be worth noting that “induction” is often defined not only for a single turbine but also for a group of turbines (or a wind farm). My personal opinion is that the turbine-scale and farm-scale “blockage” discussed in this paper (and several other papers in the literature) should be referred to as turbine-scale and farm-scale “induction” instead.
4. Line 60: “Other research suggests that…”  I think a few references should be cited for this.
5. Equation (1): Please mention what the suffix “WOA” stands for.
6. Figure 4 (and other similar figures): Please explain more explicitly what “at hub height” means. I guess these contour plots of wind speed reduction are on the surface that is 115 m (hub height) above the ground everywhere, i.e., this surface is also curved if the ground is curved, but this is not very clear from the figure caption or the main text.
7. Table 1: The power coefficient CP presented here is a “turbine-scale” CP defined based on U_inf,disk (Equation 3). But I think it would be informative to also present a “global” or “overall” power coefficient (say, CP,global) defined based on a single reference wind speed (e.g. 9 m/s) that is the same for all cases, as a metric for the overall farm power.
8. Line 426: Here it is noted for the first time that the main difference between Cases J and L is the prescribed geostrophic wind speed. I think this information (geostrophic wind speed) should be included earlier in Table 1.
9. Line 449: “the lower wind speed case exhibiting hill-induced gravity waves with longer wavelengths”  Is this correct?  It looks like Case K has a “shorter” wavelength.