General Comments:

This manuscript describes combining wind-wave coupled modeling using the COAWST modeling system with an LES modeling approach, using multiple nested grids extending down to less than 10 m horizontal resolution.  When available, model output is compared to that from the RUNE offshore dataset.

The simulations are ambitious, and it is impressive that reasonably realistic results were generated.  However, it seems the sensitivity of the model setup versus coarser scale setups are quite modest, and as the authors note, the largest sensitivity appears to be due to a shortcoming in how the LES reproduces vertical shear near the surface.

Though understandable for the large range of scales, the jump from the finest-scale mesoscale domain to the coarsest scale LES (D03-D04)  uses an 11:1 nesting ratio, which is quite extreme, and ensures that most of D04 has underdeveloped turbulent eddies.   Furthermore, D03 and D04 seem to be the focus on much of the analysis.  While the authors note the problem and show how the cell perturbation method  can at least partially mitigate against it, the vertical / horizontal aspect ratio of the grid spacing of D04 also being about 10:1 can cause distortions of the LES results, as the authors note on Line 228.

Though I’m not sure of the additional computational expense that would be involved, I’m wondering why more analysis wasn’t at least done with D05, which is an LES domain that can at least benefit from the eddies generated on D04 through its boundary conditions.  Or alternatively, why an additional mesoscale domain wasn’t used with resolution intermediate between D03 and D04.

Though the presentation is mostly clear, there are a few sections where better description / justification of the procedure should be provided.  At a minimum I would like these addressed before the manuscript is accepted for publication.

Specific Comments:

Line:  129:  ‘9 min/km’ is recommended for radiation – but does this mean that all domains update radiation at different times? 

Line 146:  ‘The CPM method…introduces controlled perturbations.’  Controlled perturbations of what?

Line 150:  I think that SWAN is not a phase-resolved wave model, but for the finest resolution WRF-LES domains, the grid spacings are certainly on the order of the wavelengths of the water waves.  Could some discussion of the implications of this be provided?

Line 167:  I would be curious to know what were the computation time / expenses of these simulations.

Line 192:  textual issue

Line 205:  Why would excessive vertical wind shear explain the change in wind direction?  Shouldn’t it affect v as well as u?  Does the explanation involve an assumed Ekman-spiral type force balance?

Line 214:  ‘mean value’ – can you clarify how the mean value was computed?  Specifically, was a horizontal average over the LES domain performed, or was just a model time series at one location used?  The horizontal average would be more consistent with the standard LES definitions of resolved / SGS, and should be provided if available, (though of course this method usually isn’t available from point measurements, necessitating some Taylor’s-hypothesis assumptions).

Line 241: ‘closely matches’ – I might say ‘more closely matches’ instead.  The LES with CPM is certainly much closer to the measurements than the other models, but over the time scales where observations exist (down to 20 minutes) LES-CPM is still generally about one-third smaller.  For timescales from 20 minutes down to about 10 minutes LES-CPM very well could be much closer to reality, but unfortunately there are no measurements there.

Review of Hamzeloo et al. (2026)

Summary:

This study investigates wind-wave interactions within the marine atmospheric boundary layer during a North Sea storm event using a multiscale coupled modeling framework. Large eddy simulations embedded within the WRF model are coupled with the SWAN wave model through the COAWST system, spanning six nested domains from mesoscale to LES resolution. The coupled simulations are evaluated against metocean and lidar observations from the RUNE campaign. Results indicate that the coarsest LES domain outperforms the mesoscale output in representing low-level wind speeds, while both domains tend to overestimate winds aloft. Wave parameters show improved agreement with observations when forced by LES rather than mesoscale output. The coupled simulations also exhibit enhanced turbulence fluxes compared to uncoupled runs, highlighting the role of wave-induced surface roughness in shaping boundary layer dynamics under storm conditions.

Overall assessment:

Overall, this study addresses an important topic in marine atmospheric modeling and presents a detailed coupled modeling approach with evaluation against observations. The paper offers insights into wind-wave interactions and the potential benefits of two-way coupling for turbulence and wave representation. However, several concerns remain regarding the interpretation of results, including the reliance on a single observation location, limited runtime for fine LES domains, potential numerical artifacts due to extreme nesting rations, and speculative claims about turbulence improvements without direct observational validation. Additional discussion of model limitations, sensitivity to wind-wave misalignment, and omitted physical mechanisms explaining how atmosphere-wave interactions differently influence boundary layer processes, winds, and turbulence would strengthen the generalizability and physical interpretation of the findings. I suggest publishable with major revisions, as the manuscript is scientifically interesting and methodologically rigorous but requires substantial clarifications and contextualization to support its conclusion fully.

Major comments:

• The authors concluded that their findings demonstrate the benefits of high-resolution coupled modeling for capturing offshore boundary layer dynamics and improving turbulence representation. However, the discussion suggests that the apparent improvement in wind may arise for the wrong reason (excessive wind shear induced by SGS). Moreover, no direct turbulence measurements were available to assess the accuracy of the simulated turbulence fields. The analysis is based on a single observation location, and improved representation of vertical wind profiles, particularly at low levels, cannot be assumed to generalize to other cases. In addition, the claim of improved turbulence representation in the coupled system remains speculative without observational validation. While the results indicate that coupling increases turbulence intensity and alters its vertical distribution, it is unclear whether these changes constitute a genuine improvement in physical realism.
• Lines 85-86: The authors justify the selection of the 5th of December based on the 'good wind-wave alignment' observed for nearly a full day. While this provides a clean case for investigating coupled dynamics, the physics of air-sea momentum exchange can differ significantly during periods of wind-wave misalignment, which are common during the rapid intensification and frontal passage of ETCs. Specifically, surface drag and the resulting LES wind profiles are known to be sensitive to the angle between wind stress and wave movemement. Could the authors discuss how the model performance or the importance of the two-way coupling might change during the periods of misalignment seen before or after the 'gray-marked' window? A brief sensitivity analysis or at least a discussion of this limitation in Section 4 would help strengthen the generalizability of the findings.
• The authors utilize a two-way coupled WRF-SWAN system but do not activate the ocean model (ROMS) within COAWST. In a shallow shelf sea like the North Sea, storm-induced surges and tidal currents can significantly modify wave steepness and, consequently, the surface roughness calculated by the WBLM. Furthermore, storm-driven SST cooling can influence the heat fluxes and stability of the marine atmospheric boundary layer. Could the authors clarify if the influence of surface currents and dynamic SST was assessed, or discuss the potential impact of neglecting this oceanic feedback on the resulting wind profiles?
• The domain configuration (Table 1) utilizes a nest ratio of 11 between D03 (1.1 km) and D04 (100 m). Standard practice typically limits nest ratios to 3:1 or 5:1 to maintain numerical stability and ensure a smooth energy cascade across the 'grey zone.' Could the authors justify the use of such a large jump? Specifically, have they assessed whether this ratio leads to numerical artifacts at the domain boundaries or a delay in the spin-up of resolved turbulence in the LES domains?
• The authors provide a detailed description of the SWAN configuration, including whitecapping and depth-induced breaking. However, there is no discussion of non-breaking wave-induced mixing or sea spray effects, both of which can influence wind speeds and sea states. In addition, initializing the open boundaries at zero may neglect pre-existing swell energy that could influence the wave field and associated wave-induced stress. Could the authors clarify whether these processes are accounted for in the WBLM or WRF physics? If not, a discussion of how their omission might affect the simulated wind profiles and surface drag would help contextualize the results. At minimum, these limitations should be acknowledged in the manuscript.
• Lines 169-173: The validation approach using D03 (finest mesoscale) and D04 (coarsest LES) against RUNE observations is reasonable, as these domains have sufficient runtime to provide meaningful comparisons. However, the analysis of turbulence fluxes in D05 and D06 is limited by the very short runtime of these fine LES domains. Early spin-up and underdeveloped turbulence, especially given the extreme nesting ratios, may affect the representativeness of the results. The authors should clarify this limitation and discuss how it might influence the conclusions drawn from D05 and D06.
• The turbulence statistics in Figure 6 suggest that the D04 (100 m) domain may not fully function as a true Large-Eddy Simulation. The resolved vertical variance (<w'w'>) in Figure 6c is very small for D04, indicating that much of the momentum transport is handled by the SGS. This is consistent with the authors’ observation that the agreement with lidar at 40 m could partly result from SGS-induced shear rather than fully resolved turbulence. Additionally, the peak of horizontal variance occurs at 70 m in D04, compared to 30 m in D06, suggesting that the 100 m grid may be too coarse to fully capture the near-surface turbulence structure. It would be helpful for the authors to clarify whether the D04 results should be considered LES or are effectively a high-resolution mesoscale simulation with significant SGS contribution.
• The authors discuss ocean wave–induced surface roughness and its associated processes multiple times, but they do not show how surface roughness differs between the coupled and uncoupled simulations. It would be helpful to include the distribution of surface roughness length for D04 and D03, either in the main text or in the supplementary material.
• The authors note in Figure 6 that turbulence levels (velocity variances and covariances) increase when wind–wave interactions are included. While previous work is cited to suggest this behavior is expected, the manuscript does not clearly explain the physical mechanism behind this enhancement for the specific North Sea case. Could the authors clarify whether the increased turbulence is primarily driven by higher effective surface roughness from the WBLM, or whether it results from dynamic feedback between the resolved wave-induced stress and SGS? Providing this mechanistic context would strengthen the paper by moving beyond observation toward a more robust physical interpretation.

Minor specific points:

• I suggest swapping Figures 1 and 2 and referring to the map in Section 2.1. The manuscript currently discusses the observed wind and wave characteristics before clearly identifying the observation location. Since these characteristics are highly location-dependent, presenting the map first would improve clarity for the reader.
• Line 123: How frequently is the SST (OSTIA) is updated?
• Line 193: Please revisit this to ensure the description is a complete sentence.
• Figure 4: It took some time to fully understand this figure. The authors may consider revising the figure caption and possibly renumbering the panels to make it more intuitive and easier for readers to interpret.
• Figure 5: Please correct the typo in the time label from 7:00 UTC -> 17:00 UTC.
• figures: To avoid confusion, please consider adding the domain number next to each experiment in the figure legends