the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 19 Nov 2024
Effects of Warming and Stratospheric Aerosol Injection on Tropical Cyclone Distribution and Frequency in a High-Resolution Global Circulation Model
Abstract. In recent years, as global circulation models (GCMs) have increased in spatial resolution, increasingly realistic tropical cyclones (TCs) and TC distributions have emerged from them. Where prior research on TC climatologies has relied on proxies like Potential Intensity (PI) and synthetic storm models, the cyclones emerging from the dynamics of newer GCMs can now be analyzed directly, using native model variables.
Such direct analysis may be particularly useful in studying possible global storm distributions under radically altered future climates, including high-emissions warming scenarios, and even those shaped by climate interventions. These interventions include various directed changes in global albedo, such as Stratospheric Aerosol Injection (SAI), with only limited precedent in the historical period. GCMs simulating realistic climate intervention scenarios, have not as of yet paired storm-resolving resolution with realistic intervention scenario construction. This has left gaps in our understanding as to how interventions might affect global storm/TC distributions.
In this paper, we utilize a new high-resolution model configuration to conduct experiments examining the effects of SAI, on tropical cyclones and global storm physics more broadly. These experiments are constructed based on prior work on SAI, using the GLENS GCM ensemble. Our analysis centers on 3 10-year experiments conducted using 30-km grid spacing. These include a recent-past calibration run; the Intergovernmental Panel on Climate Change climate pathway SSP (IPCC, 2021), for the years 2090–2099, with no SAI; and SSP 8.5, with SAI having begun in 2020 to maintain a global temperature rise of no more than 1.5 °C, also simulated for the years 2090–2099. With the resulting data sets, we deploy a novel TC-tracking algorithm to analyze resulting changes in storm tracks and properties. Based on our results for these different scenarios, we find that SAI, while in some ways restoring global storm patterns to a pre-warming state, may also create unique basin-scale TC distribution features and pose novel related hazards.
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RC1: 'Comment on egusphere-2024-3526', Anonymous Referee #1, 23 Dec 2024
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General comments
In this study, the authors look at the effect of injecting aerosols into the stratosphere on the distribution and frequency of tropical cyclones in the SSP5-8.5 scenario. For their study, they conduct and compare three simulations with the EarthWorks model: (1) a control simulation for the period 1990-1999, (2) an SSP5-8.5 simulation from 2090 to 2099 with forcings from CMIP6 and (3) an SSP5-8.5 simulations with stratospheric aerosol injection (SAI) from 2090 to 2099. While the question raised by the paper certainly falls within the journal’s scope, it is not at all clear where the new scientific contribution lies. This is down to the issues including the following: a convoluted writing style lacking structure, an introduction that does not clearly define and state the research gap, a lack of precision with scientific terms, a lack of references and claims that are questionable at best and untrue at worst (see below for more details). For the above reasons, it was extremely difficult to read the paper and pinpoint the new scientific contribution. Overall, the paper is of poor quality and should be rejected in its current form. I am extremely surprised that the paper was not rejected earlier.
The main hindrance to evaluating the scientific merits of this paper is the convoluted writing style and structure. The introduction is far too long. Dividing the introduction into subsections is also highly unusual and unnecessary for a research article. The paper also suffers from repetition in many places (see detailed comments for examples) and I suspect that the length of the paper can be reduced by at least half by removing unnecessary repetitions. While putting results in the context of the existing literature is an essential part of any scientific work, excessive citation of results from other studies in the analysis section makes it difficult to distinguish the authors’ own results from those of previous studies. I suggest the authors substantially shorten the introduction and remove the subsections. For the analysis section, the paper would benefit from a clearer separation between results and discussion. I suggest limiting the description of the authors’ own work to a results section, whereas comparison with results from other people’s work should be limited to a discussion section.
By not clearly defining the research gap in the introduction, the reader is left wondering as to what the new scientific contribution is. To be frank, the introduction reads more like a review paper than a research article; the introduction deals with several broad topics one after the other rather than honing in on a research gap. As a result, the last two paragraphs in the introduction describing the work done in this study appear out of place and do not follow naturally from the preceding paragraphs. At the end of the introduction, I did not understand why the authors had chosen the EarthWorks model in particular and the three simulations. I was also expecting a treatment of the literature dealing with the effect of stratospheric aerosols on TC distribution and frequency in the current climate, before discussing the effect of stratospheric aerosol injection in the future climate. I find it very odd that the authors do not touch upon the work done on the effect of volcanic eruptions on TC distribution and frequency.
Another major issue I have with this paper is the lack of precision with scientific and non-scientific terms. At several points in the paper, the term ‘significant’ is used to mean important or substantial. However, the term should be reserved for the statistical definition of ‘significant’. Another example is using the term ‘mechanism’ to describe a correlation without any reference to the underlying physics. Also, the term ‘explain’ is incorrectly used in many places where two variables correlate as might be expected. However, a correlation without any context and supporting evidence does not explain anything, let alone an underlying mechanism. More examples are listed in the specific comments below.
Although the authors excessively cite several papers throughout the manuscript, there are many places where references are required but not provided. No reference is provided for the EarthWorks model nor the Community Earth System Model, compromising the reproducibility of the authors’ work. At another point, the authors assert that this study ‘constitutes among the first attempts to directly model tropical storms in high resolution under climate intervention’. What were the previous attempts? Elsewhere in the text, one reference is described as ‘the literature’. I very much doubt that one paper alone can ever represent the entire body of scientific work. Without reference or evidence, the authors claim that the ‘TC pressures in EarthWorks outputs map more closely to real-world distributions..’. Further examples are detailed in the specific comments below.
The paper makes a series of questionable claims. In my mind, the most serious is the claim to have developed a novel tracking algorithm. Upon closer inspection, the authors themselves state in section 2.3 on the PHAST tracking algorithm that they ‘update an existing tracking algorithm.’ As far as I can make out, their modification to the existing tracking algorithm consists of converting the central pressure low to a wind speed via an empirical relationship between max wind speed and the central pressure. They then apply constraints on both the original wind field and the derived wind field. I fail to see how this modification results in a novel tracking algorithm. Fundamentally, the algorithm still depends on the near-surface wind speed and mean sea-level pressure, which is also the case for numerous other algorithms. Moreover, no real evidence is provided that the tracking algorithm does better than existing algorithms. The authors should remove the claim that the tracking algorithm is novel, not least because it does not properly credit the work of those who developed the original algorithms. Instead, they should characterise the algorithm as a modification/rehash of existing algorithms.
Finally, the paper suffers from a lack of discussion of limitations and errors. More details in the specific comments below.
Specific comments
L17-19: In what way exactly does SAI restore global storm patterns? And what is meant by novel hazards? Please be more specific.
L22: Strictly speaking, Emmanuel’s theory applies to a mature, axisymmetric TC in a steady state.
L29: What do you mean by available energy? Can you define this?
L41: What is the physical structure of a TC. Do you just mean the structure of the TC circulation? Or are you referring to small-scale processes, such as convection, that are not sufficiently simulated in coarse resolution simulations?
L50: Parsimonious means stingy and unwilling to spend money. However, I have absolutely no idea what a parsimonious relationship is. Do you mean a ‘tenuous’ relationship? Please select an alternative term that is appropriate for the context.
L50: What attributes are you referring to with the term ‘TC behaviour’? And how is ‘TC behaviour’ related to model skill? How do you define model skill?
L52: Tracking TCs in GCMs is standard practice. There is no need to use the term ‘direct’ here.’ It sounds like you are trying to articulate the advantages of using GCMs that explicitly resolve TCs.
L53: Define the term non-canonical cyclogenesis.
L66: Having read the paper, I fail to see how the tracking algorithm is novel.
L77: If you cannot quantify what you mean by ‘perhaps considerably’, please remove these two words.
L84: ‘Produced TC tracking results’ sounds like Bhatia et al. (2018) were testing tracking algorithms. However, this is not the case.
L88: Is it not obvious that TCs arise spontaneously? How else would they arise? I guess you are saying that they are not seeded in the simulation.
L94: What mechanisms for TC intensification are you referring to here? Why would one assume that the mechanisms for cyclogenesis would be similar when there exists no theory that can explain why we see different numbers of TCs from one year to the next?
L95: Again, I do not understand what is meant by a parsimonious relationship.
L96: Why do you refer to ‘a physics of TCs’? The field of physics is not different from one regime to another. Are you talking about mechanisms of some sort here?
L107-115: Yes, it is true that factors such as SST and vorticity feature in genesis indices and that these are empirically derived. Precisely for this reason, they have limited applicability to modelling studies, with the correlation between model TCs and genesis indices varying across models. Please mention this.
L114: Reference required for statement that such indices may not hold in future climate.
L116: Is this correlation positive or negative? What do you mean by a robust correlation?
L133: What are feedback algorithms?
L148: Why may the SSP5-8.5 be unlikely? If the scenario is unlikely, why do the authors focus on SAI in this scenario?
L168: What is loft SOO2?
L175: Since Kerry Emanuel’s theory of TCs being a carnot engine applies to a steady-state, mature TC, does it really make sense to invoke this theory for TC formation? What is exactly is the heat engine understanding of TC formation and propagation?
L175: Again, I do not know what a parsimonious relationship is.
L176-177: Please avoid using phrases such as ‘volcanism/sulfur’ and ‘hypothesized/observed’. As a reader, it is not my job to decide how to apply each word to the context.
L179: What do you mean by unexpected mechanism? What is the ‘simple SST-storm relationship’?
L191: Why say ‘may robustly extend to TC activity’ rather than ‘may extend to TC activity’? The word ‘robust’ is automatically negated by the word ‘may’.
L191: In which hemisphere is the SAI deployed?
L196: Why are the results contradictory?
L198: What exactly are heat-engine effects? I have never heard this term before. Do you just mean an increase in SST? If so, then say that.
L200: You refer to mechanisms without explaining the underlying physics that lead to the correlations that you describe. Without any explanation of the processes behind changes in the ITCZ and TC distributions, one can only really talk of correlations and not mechanisms.
L201: Is it not obvious that similar processes affect the distribution and frequency of TCs in the event of volcanic eruptions and aerosol-based interventions. After all, aerosols can be released into the stratosphere in both cases.
L203: Please remove the reference to prediction. The term prediction is reserved for forecasting. You cannot predict storm responses to SAI in the years 2090-2099. Instead you are trying to better understand the response of TC distribution and frequency to SAI.
L204: What effects and relationships are you talking about here? Please be more specific.
L205-212: Here you list a series of relationships or processes without justifying why they are being singled out for examination. There is also no description of how exactly you ‘will attempt to link any model-observed changes in TC statistics to one or more of theorized mechanisms’. I fail to see how looking at these various processes in your own simulations will provide a ‘framework’. At the most, looking at these processes will provide insight into the mechanisms behind the changes in TC distribution and frequency linked to SAI in the SSP5-8.5 scenario. The word ‘framework’ overstates the importance of your work.
L213-218: Again you are overstating the importance of your own work. I suggest you tone down the claim that you are in a position to ‘create outlines of potential TC hazards with salience well beyond the results of these specific runs’. Firstly, your study is conducted using a single model and single realisations, so the claim of applicability beyond the EarthWorks model is questionable. Secondly, this study is not about characterizing or quantifying TC hazards but the broad changes in TC distribution and frequency.
L219: Please provide reference for EarthWorks model.
L220: What are these new multiple techniques? The tracking algorithm itself is modified but not novel.
L229-230: Again, please provide a reference for the EarthWorks model.
L231: Mentioning 4-km horizontal grid spacing here is misleading, because the actual grid spacing for the simulations conducted here is ~30 km. Information about project goals do not belong in this paper, unless they are relevant for the study at hand.
L236: Please provide a reference for the Community Earth System Model. Please also Otherwise, it is impossible to ascertain how the EarthWorks
L243: Why are the MPAS dynamical cores notable? Are they better than the dynamical cores of other models? How is this relevant for your study?
L247: What metric are you using to come to the conclusion that the horizontal grid spacing yields realistic numbers of TCs. What is a realistic number and what is not?
L252: Please define ‘dynamical simulation properties’. Or are you referring to the dynamical core?
L254: What are scenario presets?
L255: So if SST is prescribed, then EarthWorks is an atmosphere-only model with no ocean component. This should be made clearer earlier on.
L256: We already know that SST is important for TC formation. Is it necessary to repeat this?
L258: How can ocean cooling be self-limiting? Firstly, I believe you mean sea-surface cooling. Secondly, the ocean cooling is not limited by the ocean cooling.
L266: What exactly do you mean by ‘likely before most appreciable change in climatic TC influences’? What climatic TC influences are you referring to. What do you define as appreciable change?
L274: Why is ‘Analysis’ capitalized.
L279: What are storm-generating SSTs? This is not a standard term.
L280: ‘Reduce/alter’. Which one is it?
L281: You say that this study ‘constitutes among the first attempts to directly model tropical storms in high resolution under climate intervention, and the first to [do] so utilizing a realistic SAI regime’. Have you discussed the previous attempts and referenced them in the text? What do you mean by a realistic SAI regime?
L284: I do not understand the term ‘storm-generating resolution’. Resolution itself does not generate storms. I think you mean ‘storm-resolving resolutions’.
L289: I am confused as to how one paper (Knaff and Zehr 2007) constitutes ‘the literature’.
L294: How do you determine that ‘TC central pressures in EarthWorks outputs map more closely to a real-world distribution’ compared to max winds?
L322: Please quantify what you mean by the track numbers being ‘virtually unchanged’ with the filtering? Otherwise, please remove this statement.
L328: How does filtering out storms weaker than category 1 increase the reliability of the best track data? Please explain or provide references. I guess you are alluding to the tracking of tropical storms (< category 1) being associated with larger errors compared to stronger storms.
L334: How do you define high fidelity here? From what I see, the model does a reasonable job. ‘High fidelity’ is an overstatement of the model’s ability to capture ‘historical TC behaviour’. The 605 TCs in the model is more than 10% more than the 517 in IBTrACS.
L343: The assertion that the model can simulate the full spectrum of intensity is misleading. The model can simulate the range of central low pressures including for category 5 storms. However, the model does not actually simulate maximum wind speeds corresponding to category 5 storms. Therefore, it is incorrect to claim that the model can simulate the full spectrum of intensity.
L343: What are downward intensity biases
L348: The order of the figures should correspond to the order in which they are introduced in the text. Why are Figure 4 and 6 mentioned before Figure 1, 2 and 3?
L349: Define observational data rounding.
L351: The term ‘great affinity’ again overstates the agreement between model and observations.
L355: Are these differences in lifetime due to the tracking algorithm or the EarthWorks model generating TCs further east compared to observations?
L360: What does CAT1 + IBTrACS mean? Are you averaging over the EarthWorks TCs and IBTrACS TCs?
L371: ‘Donuts’ is not an appropriate term to describe the TCs.
L373: What are ‘fundamental storm physics’?
Figure 1: It is strange to see a U10 plots with wind speeds corresponding to category 3 and be told that one is looking at a category 5 storm. Why do we need to convert pressure to wind speed using the wind-pressure relationship? Does it not make more sense to conduct the whole analysis using the mean sea-level pressure instead. Converting pressure to wind speed adds another level of abstraction to this study and makes it harder to interpret what is actually going on. Also, is there any reason to believe that the current, empirical wind-pressure relationship will hold in the SSP5-8.5 scenario?
L398: You say you see a significant correlation between RI and lifetime maximum intensity. I don’t. Please provide evidence of this statement. Either here or in the supplementary materials.
L401: How can rapid intensification drive storm development? Isn’t rapid intensification storm development itself?
L405: What is ‘modeling/earlier’ literature supposed to mean?
L411: Are you using ‘significant’ in the statistical sense? If not, please remove this word.
L415: What is a parsimonious relationship?
L421: What is a ‘linear part-way state’?
L426: I do not understand what ‘confounded’ means in the context of results.
L428: Why is this result unexpected? Using the term unexpected creates false expectations as to the importance of this result.
L428: You mean section 5 not Chapter 5, right?
L433: You say results of a similar magnitude were found by Bacmeister et al. (2018). What were their results?
Figure 2: The font size is too small.
Figure 4: If you want to compare the track numbers for the different simulations and IBTrACS, would it not be better to plot track density rather than the individual tracks?.
L444: How can you describe the emergence of TC activity in the South Atlantic as novel if TCs have already occurred there in the past? What exactly is the novel aspect here?
L446: Please provide a reference for the lack of TCs forming in the South Atlantic.
L452: Why are you generalising increasing TC activity in the South Atlantic to other ‘regions of the world’ without evidence to support this statement?
L457: Please specify what you mean by thermal energy. Are you referring to higher SSTs? Larger moist static energy? Or larger enthalpy?
L459: I do not agree with the statement that very few places experience an increase in TC frequency. What about the increase in the Pacific evident from the red contours there?
L463: What is the BRACE signal? What does BRACE stand for? Can you quantify the degree of correlation.
L469: How do you define ‘significant density’?
L470: What does ‘69 over the decade’ mean? Is this an increase or a decrease? Also, this number is meaningless without stating how this change relates to the absolute number of TCs in the historical scenario.
L473: Is the result robust? If not, please remove baseless speculation about the result being robust.
L476: What is a consistent correlation across scenarios? Do you mean that the ENSO index is very different between the three simulations, which makes it hard to attribute any differences in TC numbers to ENSO?
Figure 6: Font size is too small.
L478: Please define ‘relative global storm distribution patterns’. ’How can simulations share something that is defined as being relative?
L482: Please quantify what you mean by ‘matching’.
L485-488: You say that translational speeds are largely unchanged. But isn’t largely unchanged the same as saying a small change? ‘Largely unchanged’ is not sufficiently precise a term here.
L498-501: Why do refer to ‘polar amplification’ and ‘mid-level shear’ when you have not shown figures of polar amplification and mid-level shear in your results?
L512: Again, I do not know what heat-engine effects are.
Figure 8: Why are you plotting weekly TC frequency? Monthly frequency is standard and would be easier to compare with other studies?
L516: TC formation is not only dependent on SST, but a range of environmental factors.
L521: You refer to ‘overall hemispheric trends’, but it looks like you are referring to differences not trends.
L525: Why would a change in storm lifetimes affect the monthly distribution of TC frequency?
L526: Change ‘Chapter 5’ to section 5.
L529: What do you mean by ‘dynamically calculated land temperature patterns’?
L532: What do you mean by ‘global storm activity’? Are you referring to TC frequency? Or accumulated cyclone energy (ACE)? And how can you be sure that ‘significant’ increases are likely if only the global surface temperature changes?
L532-534: I do not understand what you are trying to say here.
L535-545: You talk about the effect of changes in SST on the distribution of TCs without any Figure or Table to back this up. Delete this text if you cannot back up these claims.
L549: What is a history-agnostic ENSO index?
L550: Above what SST value is convection permitted?
L553: What do you mean by ‘important new modalities’?
L556: Please provide references for the ocean upwelling argument and the permanent El-Niño arguments.
L559: What exactly is driven by a shift toward much more powerful positive-ENSO events? How can I assert from Figure 9 and 10 that the positive-ENSO events are ‘much more powerful’?
Figure 9: Caption makes no mention that SST anomaly is plotted. Which two simulations are used to calculate the SST anomaly? What does ONI stand for?
L562: What does ‘perhaps entirely’ mean? Please leave out baseless speculation.
L565: Do not ask the reader to check the long-term historical index values calculated in another study by themselves. Provide the comparison in the text.
L569: What does ‘provide an opportunity for this difference in scenario responses’ mean?
L571-576: How is this information about Atlantic TC activity relevant to your results?
L580: Where are these maps that you have produced? Presumably in Figure 11, 12 and 13?
L585: How are the changes ‘profound’?
L593: What is strong local forcing? Forcing of what?
L595-598: Why do you talk about the ‘Australasia storm development region’ and not the other regions. Stick with the global picture or discuss all regions. Why do you use ‘significant’ here if it is not used in the statistical sense?
Figure 13: I find this Figure with a different colorbar scale very misleading. The CIN values are much smaller than the values with the corresponding shades in Figure 11 and 12.
L606: Please be specific what you mean by ‘extreme’ degree of suppression.
L610: You assert that substantial increases in vertical shear in the southern hemisphere ‘can more than explain substantial reduction in SH storm activity’. Yet you cite this result from another study and you do not consider other environmental factors, such as relative humidity, vorticity etc… Please remove the word ‘explain’. You can assert that your results are consistent, but your results do not support the claim that vertical shear changes explain reductions in SH TC activity.
L613: This is another example of a juxtaposition of two words that are meaningless together. What do trends that ‘potentially most exemplify the complexity of cyclogenesis controlling factors’ mean. Either they exemplify the complexity or they do not.
L615: What do you mean by ‘powerfully’?
L618: Define ‘main-season SSTs’
L621: We already know that higher SSTs are more conducive to TC formation. Is it necessary to repeat this again?
L623-624: I don’t see a substantial expansion of a high-CIN region in the western North Pacific. Figure 11 does not display high CIN values here and Figure 13 is misleading with a different colorbar scale. Why do you not apply a consistent definition of what constitutes a high CIN value across all ocean basins?
L626: What do you mean ‘by NH standards’. Please quantify this statement.
L268: Again, ‘could more than …’ is meaningless.
L629: What is the difference between the being ‘likely the primary explanation’ and ‘one possible explanation’. Your wording is overstating the confidence of your results.
L630: What is a dominant explanation? How do you define dominant? How do your results show that this is the case?
L635: I do not understand this sentence at all.
L637-640: This paragraph is not relevant to your results.
L641: You have not examined the results with different paradigms. Instead, you have looked at individual relationships between various variables and processes, such as ENSO, and TC distribution and frequency.
L643: ‘Novel’ here is redundant as results are, by definition, always novel. Please articulate what is the novel contribution of your study to the field.
L643: What are resolved TC physics? And how can a scenario be realistic?
L645-650: I have serious reservations about the novelty of this tracking algorithm. It is not clear why the tracking algorithm features in the conclusions, as it has brought clear benefit to the study.
L651-654: This is not new information and does not belong in the conclusions. Also, you are grossly overstating the agreement between model and observations with the term ‘high fidelity’.
L656: I still do not understand what you mean by a non-linear here. Why would you expect TC frequency to scale linearly global surface temperature anyway?
L661: I am not convinced that computational power was the main limitation of this study. The main limitations stem from the limited analysis, single model, horizontal resolution and any model biases in the EarthWorks model. Please include a more comprehensive and candid discussion of limitations in the main text.
L673-679: I do not see the relevance to your work here.
Citation: https://doi.org/10.5194/egusphere-2024-3526-RC1 -
RC2: 'Comment on egusphere-2024-3526', Anonymous Referee #2, 17 Jan 2025
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In this paper, the authors "describe" (for the reason why this is in quote, see the rest of the review) the results of a set of simulations at high resolution (30km) and investigate Tropical Cyclones changes under global warming and under SAI. I am not a TC expert, therefore there are some part of the manuscript I am less likely to have good insight into, so I hope other reviewers can make up for my lack there (such as on Section 2.3).
I think the paper has the potential eventually to be very good, but there is a rather large problem that needs addressing before anything else, and that makes this paper unpublishable at this stage: EarthWorks is announced and praised, and TC results are validated, but there are no references in the Methods about the model itself. No effort is done to show results for the surface climate (what's the warming in EarthWorks under the GHG scenarios? The first phrase where warming is discussed is "In line with the bulk of prior modeling/earlier literature, severe warming in EarthWorks yields a world with fewer TCs, but a greater number of CAT5 and outlier/extreme intensity storms" but... there's no discussion of how much warming there is? How does the ITCZ look like? Do clouds make sense? Does the model has a stratospheric circulation, or if the aerosols are prescribed, what radiative code is used? What's the resulting TOA imbalance?) If this is a new model, then there needs to be a serious validation behind that can't jump straight to the TC results. The only "paper" cited about EarthWorks is a proposal to NSF as a PDF: to say this is not best practice is definitely not enough. I can't judge the maps I see about shear if I can't see what the surface temperature in this model is. The authors also don't explain how they use the forcing from CESM2: sometimes they talk about SO2, but does it means you're using the SO2 injection locations from the Tilmes et al. (2020) paper, or the aerosols forcing in 3D? How is it assimilated, and have you verified it works? If so, why are you not showing this?
In no way the way the authors present their data about a new model (also considering the lack of a data availability statement about the models result, not to mention the code) is in line with the practices outlined by ESD (or by any other reputable journal in 2025): https://www.earth-system-dynamics.net/policies/data_policy.html Their description of EarthWorks is non-existent.
With all this said, I really can't recommend anything more than a sound rejection at this point. I have other comments about the manuscript and some of the analyses (most of them positive!) but I don't think I can engage with a paper that ignores any guideline set in the last decade about sharing underlying data, model validation and transparency. If the authors have a manuscript of validation of EarthWorks (which I didn't find also by Googling, at most I found a GitHub page the authors didn't even bother adding here), they should cite it, and they should explain how the forcing from SAI works in their model (if this is a new model, even if based on CESM, they should show it in depth). Only after all of this can this manuscript, which is downstream of those, be assessed for its scientific merit.
Citation: https://doi.org/10.5194/egusphere-2024-3526-RC2
Interactive computing environment
Code and Sample Data for PHAST Algorithm Andrew Feder https://github.com/afeder17/PHAST
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