the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 14 Aug 2024
Typhoon statistics in variable resolution Asia-Pacific CAM-SE
Abstract. Three Asia-centric configurations of the Community Atmosphere Model with the Spectral Element dynamical core (CAM-SE) were set up, with horizontal resolutions of approximately 1° globally, 1° increasing to 0.5° over the Asia-Pacific, and 1° increasing to 0.25°. A typhoon tracking algorithm was developed to extract the tracks of typhoons generated by the simulations. The typhoon intensities were bias corrected using scale conversion factors calculated from a comparison of tracks extracted from the European Centre for Medium-Range Weather Forecasts Reanalysis version 5 (ERA5) and the International Best Track Archive for Climate Stewardship (IBTrACS). Typhoon frequency, track density, genesis locations, and energy were calculated from 20 years of equilibrium climate simulations using the three configurations, then compared with the statistics from ERA5 and IBTrACS. The 1° and 0.5° CAM-SE simulations were unable to produce enough “Super Typhoons” (maximum sustained central wind speed ⩾ 51 m s-1) even after bias correction. The 0.25° simulation managed to produce enough “Super Typhoons”, indicating that at least 0.25° horizontal resolution is advisable for global climate simulations to produce appropriate “Super Typhoon” statistics. The regionally refined 0.25° CAM-SE configuration was estimated to be at least two times faster than a globally 0.25° typical configuration.
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Status: open (until 12 Dec 2024)
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RC1: 'Comment on egusphere-2024-2415', Anonymous Referee #1, 11 Nov 2024
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This paper evaluates the effectiveness of variable-resolution (VR) configurations of the Community Atmosphere Model with the Spectral Element dynamical core (CAM-SE) for simulating tropical cyclones (TCs) in the Western Pacific. Using three resolutions - 1deg globally (ne30), 1deg to 0.5deg refinement (ne30x2), and 1deg to 0.25deg refinement (ne30x4) - the authors conducted 20-year equilibrium climate simulations to compare typhoon statistics, such as frequency, intensity, and tracks, against IBTrACS observations and ERA5 reanalysis. While 1deg struggled to reproduce intense TCs, the 0.25deg generated realistic statistics, demonstrating that at least 0.25deg resolution is important for TC climatology in the region. The study notes the computational efficiency of regionally refined grids.
First, I want to note that I genuinely believe the authors have put some effort into preparing this manuscript. I agree that testing VR simulations is useful. I also concur with the finding that 0.25deg does better simulating TCs than 1deg.
However, to be frank, I am unsure what hypothesis the paper is testing or the question being answered. In the abstract, the authors note that these simulations provide evidence that 0.25deg simulations can be used for global TC statistics. However, there are numerous examples of 0.25deg simulations showing this and more; there are open-source, public datasets using 0.25deg simulations with a wide range of models (e.g., see Roberts et al., papers on HighResMIP from ~2020), including 0.25deg versions of the model used here. Why did the authors need to run new simulations just to find this? What value-added exists in this deck that can benefit the community? So this falls flat to me and doesn't seem to offer a lot of novelty (or at least the authors haven't made a compelling case). Of note, the authors *do* cite some of this work, but the paper would be well-served by a better comparison versus just "this has been observed elsewhere..."
I would be more amenable to this publication if the authors were seeking a deeper understanding of the performance of the variable-resolution CAM-SE model, but there are many places (I have highlighted a few below) where they seem almost dismissive or uninterested in a deeper understanding of the configuration. Topography is merely interpolated rather than using supported tools. Timesteps are set very long, seemingly for the sake of computational expediency. Sensitivity analyses of various tunable parameters and/or settings are not used. There is also a large amount of literature regarding variable-resolution climate models that now exist (some names off the top of my head in the US are Herrington, X. Huang, Ullrich, Rahimi, Rhoades, Sakaguchi, Q. Tang, Zarzycki, but there are others) that could help with the setup/configuration/discussion here. Again, I am left wanting.
Lastly, I will also note that the paper was relatively confusing and difficult to follow due to typographical issues and grammar. I am sympathetic to the fact that the authors are not likely native English speakers, but there are many confusing passages ("evaluation of done closer to equilibrium" is one such example) that require multiple re-reads. Any revision desperately needs thorough proofreading.
As is, I cannot recommend publication. The paper needs to be more cohesive, and more care is needed to describe the modeling setup and motivate design choices. A lot of "hand-waving" has been done (which I note below) regarding model configuration and topography. The authors explain that they did not have the resources to test some assumptions but performed a rudimentary timing simulation. The actual results are relatively poorly motivated- the authors spend a great deal of time talking about a tracker that seems to combine previously published trackers but requires a lot of "massaging" to get reasonable climatologies. A lot of the results are based (I believe) on using a linear correction factor based on maximum surface wind (MSW) and 10m winds as output from ERA5 and CAM. At least some formal testing of statistically significant differences needs to be done.
In general, there really isn't anything scientific of substance resulting, with the paper reading very much as a superficial description of model output. Any revision should explicitly state how these simulations offer an improved understanding of how 0.25deg models (either VR or just such models globally in general) simulate TCs for this particular region. Added benefits would be highlighting specific situations where these simulations would be useful and suggesting potential biases to be improved by model developers.
Major comments:
Honestly, there are many things that left me a bit perplexed. I have listed some here, although this is a partial list.
Model configuration. First, the authors offload a significant amount of model description to the appendix -- it should be moved to the main text. Upon initial reading, I was pretty unclear how meshes were generated, what configuration was used, etc. Second, I have many concerns that indicate the authors may not be overly familiar with the modeling system. They use an 1800s (30-minute) physics timestep for even their 0.25deg simulations. This is uncommon in the high-resolution modeling community, where this timestep is probably almost always <=10 minutes at these scales. The authors do note that this choice was mainly for "computational speed," although then the authors make statements like "the differences most probably would not affect the results of this study" with little/no basis I can find. The papers they cite (e.g., Williamson, Reed) actually find that the timestep is an important sensitivity in model precipitation.
Topography. The authors eschew the use of the supported "TOPO" software for interpolated high-resolution data. But one of the critical aspects of the TOPO tool is to be able to differentially smooth topography over variable-resolution meshes, which the authors describe in the paper: https://gmd.copernicus.org/articles/8/3975/2015/ ... Also, the software (at least v1.0) was published almost 10 years ago, so I'm not sure about the comment, "At the time of this study, the TOPO toolkit was still under development, and we excluded its use..." -- how old are these simulations? I am quite concerned about the simulations being valid in general -- I would suspect a lot of gravity wave noise to be generated in the low-resolution part of the domain associated with the interpolated topography (i.e., investigate the mean 500 hPa vertical velocity field).
Tracking methodology. The tracking algorithm, while similar to some other published ones, seems overly complicated, as the authors note. Multiple publicly available tracking algorithms exist, two of which (TempestExtremes and TRACK) are commonly used in the field for evaluating high-resolution climate models. Why did the authors create their own? What are the benefits and drawbacks of their approach? If the results behave similarly to existing algorithms, that would be acceptable, but then the discussion of trackers can be moved to an appendix.
Wind correction. After re-reading a few times, I *think* I've figured out that the authors correct what they view as a low bias in ERA5 wind (shown in Fig. 2) by applying a linear scaling factor between ERA5 winds and IBTRACS winds and then apply that moving forward. That explains why ERA5 in Fig. 3 has typhoon+ storms, but Fig. 2 does not. This needs to be clarified, and it currently reads very opaquely. Suppose the authors are concerned with a low bias in storm intensity in ERA5. In that case, I encourage them to use sea level pressure and then some sort of pressure-wind correction rather than just using a linear correction as a bias correction.
Computational scaling numbers: I am baffled as to how the SE core at ne120 has 5x more cells than one of the VR grids but runs 9x slower. That shouldn't be the case. If anything, the additional "overhead" in the VR simulation would cause a slight penalty versus purely linear scaling (although I would hope it is minor). I suspect the authors are using a longer physics timestep for the SE ne120 runs. What they are seeing in the scaling numbers is that the physics timestep is taking more time than expected (i.e., it's not just a number of cells issue, but rather how often the cells are being calculated upon). However, given that they specifically chose the 1800s, I am not sure why it's worth discussing scaling through this lens (i.e., it makes the VR simulation look "better" on a per-element basis, but it's because they are taking longer physics timesteps, even if the 0.25deg mesh).
The comment, "Hence there would be no reason to use the SE dynamical core except for its variable resolution capabilities, " is a reasonably bold stance in a throwaway paragraph without formal timing comparisons. Aside from the fact that a handful of simulations does not a formal timing estimate make (as any high-performance computing software engineer would note), this ignores previous literature quantitatively comparing the dynamical cores with respect to numerical diffusion and weak/strong parallel scalability.
I encourage the authors to read papers such as:
- Dennis et al., 2011 --> https://journals.sagepub.com/doi/10.1177/1094342011428142 -- authors show local SE method has much better parallel scaling than FV.
- Evans et al., 2013 --> https://journals.ametsoc.org/view/journals/clim/26/3/jcli-d-11-00448.1.xml -- authors show SE has a better "effective resolution" than FV.
Other comments:
Line 181. Why is Bluestein (1992) (a synoptic meteorology textbook) being cited for "the central difference method"?
Line 294. "In the discussion that follows, values are considered different if their ranges extended by standard deviations do not overlap." This is confusing, but my reading of this is if the -1 STD to +1 STD range for variable A and variable B differ, they are considered statistically significantly different. However, no significance testing is performed following this statement that I can find.
Line 446. "The latitudinal bias may be partly explained by the location of the annual mean subtropical high in the simulations." The authors produce no evidence of this statement.
Line 489-490. I cannot find a good explanation as to why the authors analyze two overlapping time periods (2001-2020, 2011-2020). As best I can tell, the 2011-2020 period was chosen because that was all the ERA5 data the authors had available, but they ran the model simulation from 2001-2020. If that's the case, why wasn't the ERA5 data analyzed back to 2001?
Line 636. "Warm start" in a modeling sense usually means a balanced and/or assimilated state. These would be more like a "cold start" simulation. I am not sure what a "cold start" aquaplanet simulation means in this context.
Citation: https://doi.org/10.5194/egusphere-2024-2415-RC1
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