Please sea the detailed comments in the attachment.

The authors designed an idealized numerical model setup to mimic the South China Sea (SCS) and its connection with the west Pacific Ocean in order to understand the control of the slope topography in the three-layer circulation system in the SCS. 

In my opinion, the numerical design is too simplified to reflect the complexity in the interactions between the three layered circularions, the setup is flawed and does not provide convincing results to support their quantitative conclusions.

The major flaws of the numerical setup are listed below:

1. The depth of the west pacific ocean is set to the same of the SCS (4000 m), and adopts the same initial temperature and salinity profile. This means that there is no density gradient in the deep layer between the pacific ocean and the SCS which is needed to form the intrusion of the denser western paficic water into the SCS and the resultant cyclonic deep layer circulation.  I don't understand how can the model reproduce this deep circulation in this case?

2. What is the reason for setting three values of Kv for surface, middle and deep water layers, respectively? There is not even a linear transition between the three values in the setting. It is unclear how sensitive is the model to such artificial setting, and whether an abrupt jump of the values at the bounday cause instability of the flows and their interactions. 

3. The simulation is run for 25 years only.  This is probably sufficient for a shallow shelf sea but is definitely too short for the SCS and west pacific ocean to develop a stable or quasi-stable states of the circulations, especially for the middle and deep layers. This means the system is still in a fast developing phase with instable states, and I have serious concern on using the results for quantative analysis of the three-layer circulations. 

4. It seems the authors mix the desciptions of the simulation results with results from existing literature for formation of the three-layer circulations, see line 123-129. As the authors described, density differences between the SCS and the pacific ocean is needed to drive the deep intrusion, but such feature was not implemented in the model setup (see point 1).

5. It is unclear to me how the authors managed to adjust the outflux and influx at the open boundary to these exact values. My concern is that the model results may be largely driven by the speficied input/output at the boundary, rather by the internal dynamics of the system. The authors need to justity why such configuration is reasonable. For instance, it is stated that the influx/outflux was defined in the upper water layer at the southeastern and northwestern boundaries of the open ocean (line 99-100). What is set for the deeper water layers in these open boundaries, and for other parts of the open boundary in the pacific ocean? Please clarify these and justify that the system is not purely driven by the boundary setting.

Given the major flaws mentioned above, I am not convinced by the quantative numbers, e.g. 10% increase in the intensity of the middle anticyclonic circulation and 27% increase in the deep cyclonic circulation (line 299-300) given in the summary. A more comprehensive sensitivity study on how a change in the specific configurations would affect such numbers is needed. This includes not only the influx/outflux setting in the surface layer at the open boundary but also the run time, the setting of Kv and the intitial temperature&salinity profile.

Besides a more comprehensive sensitity study, I suggest the authors to perform analysis using more realistic simulation/reanalysis results that are readily available, e.g. from the global HYCOM. The multi-year averaged results (climatology) should provide a more convincing dataset for the analysis, and it has a more realistic representation of the complex topography and the three-layer circulations. A result comparison between the idealized model setup and the more realistic setup would provide more insights into the topographic modulation on the layered circulation in the SCS. 

Review of "Topographic modulation on the layered circulation in South China Sea" by Tang et al.

This manuscript studies the vertical structure and dynamics of the continental slope circulation in the South China Sea. Layer-integrated vorticity diagnostics from Primitive-Equation numerical simulations with idealized geometry are used to study the sensitivity of the circulation to the upper-layer inflow in the Luzon Strait. It is shown that the vertical structure of the circulation (respectively cyclonic, anticyclonic, and cyclonic for the top, middle and bottom layers) is linked to the surface intensified flow's interaction with the curved geometry of the marginal basin.

I see several major issues in the manuscript. Briefly, the most important ones involve the attribution of the middle and bottom layer's driving mechanisms, potentially significant spurious flows associated with pressure gradient errors in the simulations, and the quantification and interpretation of the viscous term in the model. Text and figures read generally fine, but there are English language problems in the text, and several figures lack axis labels. The major and minor points are detailed below.

Major points:

M1 (Section 2, pressure gradient errors): The known problem of spurious flow associated with numerical pressure gradient errors in terrain-following models such as ROMS always needs to be examined before a process study can be performed adequately. The authors need to show how the magnitude of the spurious circulation that arises in their model with an unforced, initially laterally-uniform stratification everywhere compares to the slope currents in their forced simulations. The physical signal of the slope currents is weak (less than 10 cm/s in the middle and bottom layers), and the spurious flow needs to be much smaller than that. With 30 vertical levels, a 5 km grid, and the O(1e-2) bottom slopes involved, pressure gradient errors are likely to be non-negligible in the SCS's continental slope. Without smoothing the topography, the only solution is to refine the horizontal and vertical grids until the spurious flow becomes negligible. This numerical effect needs to be thoroughly examined before the results can be interpreted appropriately.

M2: Related to point M1, what is the vertical spacing of the sigma levels? Are they refined near the surface and bottom to improve representation of the boundary layers?

M3: (lines 105-108): All results may be sensitive to these coefficient choices (particularly flow in the top and bottom layers). This needs to be thoroughly examined if a spatially-varying viscosity coefficient is used.

M4: Related to M3, what was the turbulent closure scheme used? This information is missing in the text.

M5 (lines 113-114): Is the system at a near-steady state at this point? Some metric such as a global KE time series should show this clearly and help determine how long the simulations need to be. Also, I assume this is a 5-year average? If so, please mention that here.

M6 (Figure 2, Section 2): The topography in the southern boundary of the LS has a more irregular shape than the SCS and Pacific parts of the domain. What is the reason for this choice, and how sensitive are the results to this geometry (compared to a configuration where the LS's southern boundary joins the interior of the SCS smoothly like what is seen in the LS's northern boundary in Figure 2a)?

M7 (Lines 176-177, Equation 1): There is no separation between the vertical and horizontal viscosity terms. It is therefore impossible to distinguish physical bottom Ekman pumping from numerical lateral viscosity.

M8 (lines 190-192, 216-217): I think it is indeed likely that the near-bottom cross-slope flow dominates near-bottom vertical velocity, but this has not been shown directly. Besides near-bottom flow across isobaths, bottom Ekman pumping can also produce important vertical velocity and vortex stretching. This effect is not examined here because the term is excluded from the analysis and from Equation 2 (the approximately equal sign is an assumption rather than a result). Figure 5c shows that bottom friction may be important in the bottom layer's vorticity budget, though it is unclear because the viscous term combines lateral and vertical friction.

M9 (lines 238-240): Source/sink Stommel and Arons-like dynamics does not include topography, so it cannot be consistent with a flow where cross-slope bottom geostrophic flow is dominating the bottom layer dynamics. The only way to test this type of dynamics unambiguously is to perform experiments with a vertical wall (as in the adjacent rectangular basin representing the Pacific) instead of a slope.

M10: Since the model has a 5 km resolution, it should be eddy-resolving in the SCS, where the first baroclinic deformation radius is around 60 km in the SCS (e.g., Figure 6 in Chelton et al, 1998 or Figure 8 in LaCasce & Groeskamp, 2020). Because mesoscale eddies and sloping topography are present, a competing theory for the cyclonic layers' flow in a basin like this is eddy-slope interaction (Neptune Effect, e.g., Holloway, 1987, see also Stewart et al., 2024 and references therein). It may be possible to test this hypothesis by changing the horizontal resolution: If by coarsening the grid spacing until eddies are no longer resolved results do not change, then an eddy-free interpretation may be correct. But if the Neptune effect is important in one or both cyclonic layers, these layers will have stronger flow with finer, eddy-resolving resolutions, and the interpretation needs to be revisited.

M11: What is the first baroclinic deformation radius in the model (especially in the SCS's deep basin, and in the SCS's slope)? This information is relevant for addressing point M10 and for comparing how well the model represents the real SCS's stratification.

M12 (lines 322-323, Data Availability statement): The repository in the DOI (https://doi.org/10.5281/zenodo.13835538) contains only *.mat files. Based on the file names, I assume these can be used to replot the figures, but they are not sufficient to reproduce the results. To ensure reproducibility, the authors need to provide all the source codes used in the calculations, as well as the configuration files for the ROMS model applications.

Minor points:

m1: (lines 30, 232, 311): The term "Cascading" is typically used to refer to a specific process driven by surface buoyancy loss. To avoid ambiguity, I suggest using "downwelling" instead.

m2 (lines 94-95): Is the southern model strait the same depth as the model Luzon Strait?

m3: Figure 1: The real topographic gradients in the SCS are more difficult to see with these color limits. It may be better to change the lower limit to something closer to 4 km, even though this would saturate the color scale in the Western Pacific troughs.

m4 (line 292): Stimulated or simulated?

m5 (line 303): "curved" is probably a better description, Since the basin is circular.

m6 (Figures 6, 7 and others): Several axes are missing labels, units, or both.

m7 (Figure 6d): It may be better to flip Figure 6d 90 degrees clockwise to have depth in the y-axis.

References:

Chelton et al. (1998): Geographical Variability of the First Baroclinic Rossby Radius of Deformation, Journal of Physical Oceanography.

LaCasce & Groeskamp (2020): Baroclinic Modes over Rough Bathymetry and the Surface Deformation Radius, Journal of Physical Oceanography.

Holloway (1987): Systematic forcing of large-scale geophysical flows by eddy-topography interaction, Journal of Fluid Mechanics.

Stewart et al. (2024): Formation of eastern boundary undercurrents via mesoscale eddy rectification, Journal of Physical Oceanography.