Review of "Characterizing atmospheric stability in complex terrain" by Agarwal & Lundquist

This paper addresses an important and timely topic: characterizing atmospheric stability in complex terrain using Perdigao tower data. The authors evaluate stability metrics with different Reynolds decomposition intervals, and quantify the predictive skill of low level vs hub height stability. They apply clustering methods to recommend a necessary number of met masts which is good but rather academic because usually the problem is the opposite: how many more met masts than 1 are needed to properly sample the site conditions (and where numerical estimates of wind field covariance are helpful - see the other general comment).

The analysis is carefully executed, the dataset is of very high quality, and the topic is relevant to both atmospheric science and wind energy.

However, the paper in its current form is incomplete. Perdigao has also been extensively studied with mesoscale and large-eddy simulation (LES) modeling, yet the study relies exclusively on observational/statistical analyses, while ignoring the context and assistance that numerical models can provide.  Without at least a discussion — and preferably some demonstration — of how models complement observations, the results risk being overly narrow and less generalizable, especially when the conclusions are drawn from data from a single site.

I therefore recommend major revision to address the points above, and a few specific comments below.

Specific comments

L32: Discussing various papers about the effects of stability before at least defining it broadly. Some of these papers even analyze data from complex terrain.

L152: The Obukhov length is not proportional to the height above the surface. It is the height above the surface.

L162: Please define Tv. Is it even meaningful to use theta-v and Tv in the context when theta is then anyway assumed to be constant?

L250: Please clarify if the linear regression is calculated at specific time-stamps? If yes, please discuss how the vertical information propagation may adversely affect this metrics.

L274, Figure 2: The case (e) tse09 (valley) stable exhibits the opposite behavior from every other case. This would merit some discussion.

L277: Not entirely clear how it is discernible from Fig. 2h that the stable ogive shifts to mesoscale fluctuations at 60 min. Do you mean that the curves which appear to have flattened, suddenly receive a kink?

L307: "more diffuse" is not the best choice of words. It would be better said that the winds are less bidirectional, or aligned with the terrain.

L310, Figure 3: Please discuss why the ogives (are they really ogives, strictly speaking?) for u* are so different from those for the heat flux?

L477: It is too optimistic to claim that this work improves the characterization of atmospheric stability. It only demonstrates the challenges, based on data from one site.

L486: "... towers that extend to hub height ...". Should they not be extended to the rotor top? Arguably, similar if not larger discrepancies will occur when the top of the boundary layer, which often is at about HH, intersects the rotor area.

Review of Characterizing atmospheric stability in complex terrain by Nathan J. Agarwal and Julie K. Lundquist

Recommendation: Major revision

This is a well written, careful study that leverages the unusually rich Perdigão tower dataset to assess how three stability metrics (Obukhov length L, turbulence kinetic energy TKE, and dissipation rate ϵ) behave in complex ridge–valley terrain and how representative surface (10 m) measurements are of hub-height (100 m) conditions. The manuscript provides useful guidance on Reynolds-decomposition windows (ogive analysis) and introduces sensible metrics for quantifying representativeness (HHPI and horizontal homogeneity). Overall the work is scientifically sound and valuable to the wind-energy and boundary-layer communities, but several important methodological clarifications and additional discussion (especially on canopy effects and comparisons to flat-terrain benchmarks) are required before publication. 

Major comments

1.    Expand and tighten the Introduction with regard to prior Perdigão work.

o    The Perdigão campaign generated many multi-instrument studies on ridge–valley and canopy effects. Readers would benefit from a clearer map of what previous Perdigão studies (and other complex-terrain works) have shown and how this manuscript’s contribution differs. 

o    Menke et al. (2019; Characterization of flow recirculation zones at Perdigão), a study co-authored by one of the present authors, also investigates stability effects and should be discussed — particularly in the context of how recirculation zones may provide alternative explanations for some of the vertical decoupling observed here and why the stability characterization approach used in Menke et al. is not used in this work. If the authors consider Menke et al. (2019) not directly comparable, they should explicitly state and justify this.

2.    Significantly expand discussion and quantification of canopy/vegetation effects.

o    Why it matters: Several of the manuscript’s central findings — in particular the apparent 10 m vs 100 m decoupling in the valley and the NE ridge — could be strongly influenced by canopy height and density. The manuscript repeatedly notes “canopy” or “canopied NE ridge” but does not quantify canopy height/cover or show photos/maps of tower surroundings. The text suggests remote generation/advection as the explanation (e.g., upside-down boundary layer / advection), but canopy sheltering is an equally plausible (and in places more parsimonious) explanation for decoupling at 10 m. See the discussion and TKE stratification text and figures. 

o    Suggested fixes:

    Add a table or figure that lists canopy/land-cover at each tower (or at least for the three focal towers), including approximate canopy height and whether the 10 m sonic is inside the roughness sublayer/canopy. 

    Include site photographs of the three focal towers (or reference an existing photo repository) to make interpretation of 10 m measurements transparent to readers.

    Re-analyze (or at least discuss) whether the valley / SE ridge 10 m decoupling is better explained by canopy effects than by remote advection.

3.    Justify the choice to focus horizontal-homogeneity (HoH) on 10 m measurements only, or extend analysis to higher levels.

o    The HoH analysis determines the minimum number of towers needed to represent site variability but is performed at 10 m because only 18 towers have 10 m temperature. For wind-energy stakeholders, representativeness at hub-height (or intermediate heights) is more relevant than representativeness at 10 m. 

o    Suggested fixes:

    Either: (a) repeat the HoH analysis at other heights where sufficient data exist (e.g., 20/40/60 m subsets) and show differences, or (b) clearly justify why a 10 m-based HoH is still useful for turbine siting.

    Add a short paragraph discussing pros/cons of using Louvain community detection (e.g., sensitivity to input correlation metric and partition resolution) and whether other clustering algorithms were tested.

    Consider adding the widely used TRIX (or equivalent) representativeness test from the wind-energy community to complement the HoH analysis — readers from industry will find that comparison useful.

4.    Provide a direct comparison or benchmark of HHPI with flat-terrain results (or literature).

o    The conclusion that “surface measurements are unable to make hub-height predictions” is important, but the reader needs context: are the HHPI values unusually low compared to flat terrain or other published sites? That context would quantify how “bad” the Perdigão complex terrain results are and support the recommendation for tall towers. The manuscript suggests future work comparing to other sites but does not provide literature benchmarks. 

5.    Re-evaluate some interpretations of Figures (wind roses and 10 m vs 100 m diffuseness).

o    The manuscript states “100 m winds are more diffuse than 10 m”; however, the reviewer’s read of Fig. 4 suggests 100 m sometimes shows a clearer prevailing direction than 10 m. Please verify the figure interpretation and ensure the text statement is correct. 

Minor comments and editorial suggestions

1.    Introduction: Many studies cited that are not explicitly identified as flat or complex-terrain studies. For each “stability affects wind generation” citation, briefly state terrain type (flat, coastal, complex) so readers immediately see which conclusions generalize to Perdigão-like terrain. 

2.    Be consistent with units formatting: use parentheses “[m s⁻¹]” consistently instead of mixing “[]” and “()” in figure captions. (Figure 1 and others show mixed usage.)

3.    Move subplot descriptions from the long caption into a one-line title for each subplot (improves readability for multi-panel figures such as Figs. 3 -13). This was hard to follow when flipping between caption and panels.

4.    Line 140: double words “to to” 

5.    Two sentences in 3.2 (lines ~394ff) are nearly identical and can be combined for concision: the point about TKE HHPI improving with height for all sites can be consolidated. 

The paper covers an important aspect of wind meteorology: atmospheric stability. It also provides a thorough analysis of experimental data to identify trends and limitations of the different methods used to characterize stability.

The introduction provides readers with an overview of research efforts to characterize the impact of stability on turbines and wind farms. It highlights the lack of general understanding of the impact on power and wear and indicates that characterizing stability is an expensive process.

The methods section details the data sampling, equations of the indicators used (L, TKE, and ϵ), how the dataset was cleaned, and which averaging windows were used. The methods section also introduces a study on the impact of the Reynolds decomposition time (1 to 60 minutes) on heat flux and friction velocity.

The conclusion helps wind farm designers determine where to locate met masts and understand the risks of taking 10-meter wind speed measurements and extrapolating them to derive an atmospheric stability assessment, which is likely inaccurate. The authors suggest using LES in complex terrain to better identify locations where it is important to place a measurement tower and to use Louvain group theory to identify these locations, as well as to identify similarities using Python code.

Overall, the paper is well-structured and presented. However, it would have been helpful to include more justification for the analysis of the results. For example: "the plot indicates that ... because (explanation)" I provide a concrete example of this in my comment on L297.

The abstract could also be improved. It is unclear where the authors provide general information and where they present the paper's findings. Additionally, the analysis of the sampling window for heat flux and friction velocity, which occupies an important portion of the paper, is not mentioned.

Below are some general comments and questions that I recommend addressing in the paper.

- Can you define or explain the tilt correction methodology of the sonic anemometer?

- What about cloud cover? Is Perdigao rarely covered by clouds, or were cloudy days filtered out?

-- Along those lines, what is the sun exposure near the ridges and in the valley? Is it full sun between 12 p.m. and 4 p.m., or is it partly shadowed by the terrain?

Similarly, for the heat flux analysis, can the changes in sun exposure throughout the day be excluded? For example, should we expect the results between 12 and 13 hours to be the same as those between 15 and 16 hours, or should we expect some variability in e.g. the sun radiation from the ground?

- The paper does not specify the timeframe of the data. Did you select a few days or years? Which exact dates do the data represent? During the filtering process, are significant time periods (days or weeks) flagged out? What impact does this have on, for example, the 60-minute sampling? Were dummy values inserted, or were full 60-minute blocks removed?

- Regarding your use of the Louvain community detection algorithm, are any tolerances or parameters used to create the groupings? It would be useful for the reader to know what threshold was used to determine the borders between the groups.

- You mention hub height as being important in characterizing stability. On what criteria was the hub height chosen? Can stability be characterized by parameters other than turbine height, or is this choice based on the assumption that we are mostly interested in knowing what the turbine "sees"? Please explain this in the paper.

Also, I have two comments related to lines:

L62: It's unclear what is meant by "stretch into an ellipse". From where is the ellipse seen? (The wake is 3D).

L297: "unstable friction velocity ogives at all tower locations show asymptotic behavior for a 30 min averaging period and a shift to mesoscale fluctuations for a 60 min averaging period"

-> Please help the reader by explaining that this is seen by the increase in u* for the 60-min average period, or otherwise if needed.