the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 01 Aug 2023
Coupled atmosphere-ocean simulations of contemporary and future South Pacific tropical cyclones
Abstract. Tropical cyclones – TCs – affecting the South Pacific region are studied using coupled atmosphere-ocean earth system models and (offline) storm tracking software which tracks the position of simulated pressure lows through time. The models used are the United Kingdom Earth System Model, version 1 – UKESM1 – and the related New Zealand Earth System Model, the NZESM. The model pair considered here differ only in their treatment of the ocean and the NZESM has a nominal resolution of 0.2° in the region surrounding New Zealand and 1° elsewhere; UKESM1 has a a uniform 1° resolution everywhere. After validating the storm tracking algorithm against the track of cyclone Giselle from 1968 and cyclone Gabrielle from 2023 we use the Saffir-Simpson scale to split the tracked systems into categories based on their severity. For systems formed in the vicinity of New Zealand (and globally) the overall number is overestimated but stronger (category 2 and 3) storms are underestimated. We also see a general decrease in the total number of storms as radiative forcing, F, increases although there is some evidence of a small increase at extreme levels of warming. In the metrics studied here we find no difference between the ensembles of UKESM1 and NZESM simulations and going forward use the UKESM1, which has larger available ensembles. The power dissipation index, PDI, gives a first order measure of TC strength and we find that the average PDI per storm increases with F by up to 26 % under a 'fossil-fuelled development' scenario. Although the physical mechanisms behind the increase in average PDI with F are relatively simple to understand, those governing the frequency of occurrence are not. In the results shown here, vertical wind shear increases with F which tends to reduce TC numbers but the effect of the tropospheric relative humidity is much less clear. The increase in the area of the tropics bounded by the 26.5° isotherm should, on its own, increase the number of TCs, in opposition to the general behaviour observed, except perhaps at extreme levels of future warming.
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Status: closed (peer review stopped)
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RC1: 'Comment on egusphere-2023-1694', Anonymous Referee #1, 24 Jan 2024
This paper proposes a tentative analysis of an ensemble of historical and future climate projections with the UKESM and NZESM to identify potential trends in TC-related risk for New Zealand. To do so, they first validate their tracking methodology by comparing it to another similar methodology widespread in the literature. Then, they evaluate the frequency of TCs in the South Pacific basin then their intensity in the simulations. Finally, some perspective is given regarding how the results can be traced back to the simulated large-scale environment.
The purpose of the paper — a regionalized analysis of the future cyclonic activity in the South Pacific and, more particularly, for New Zealand — is an important and valuable endeavor. If they could be trusted, the conclusions in this paper would be meaningful for local adaptation to climate change. However, in its current state, the paper does not provide an analysis that is rigorous enough for any of the conclusions to be trustworthy.
First, most people well acquainted with the literature regarding GCM simulations of tropical cyclones with GCMs would be wary of the TC climatology simulated by any climate model, even more so a coarse-resolution coupled model. Two main limitations need to be overcome: coarse-resolution models are widely known for failing at simulating tropical cyclones (e.g., Roberts et al. 2020b; Camargo et al. 2013; Tory et al. 2013), and sea-surface temperature biases impact the TC climatology (Huang et al. 2021; Sobel et al. 2023). Neither of these limitations is discussed and addressed. Overall, the validation of the historical simulations barely exists. It is based on comparing the simulated TC climatology to that of ERA5 instead of observations. Although it might be acceptable in some contexts, the limitations of ERA5 itself should be acknowledged, and reasons for not using easily available observations should be provided. As such, the paper does not convince me that the model is simulating South Pacific TCs correctly.
Even if the model simulates cyclones correctly, the analyses made by the authors appear too shallow, especially since they lack basic quantitative and statistical foundations. Finally, the paper is not well structured. Only a complete overhaul of the paper and the addition of essential analyses will make it publishable.
MAJOR COMMENTS
- In its current form, the assessment of the models' ability to simulate tropical cyclones is not convincing. Here are some points of concern:
- Coupled models are known to have sea-surface temperature biases that can greatly affect the simulated climatology of tropical cyclones (e.g., Huang et al. 2021; Sobel et al. 2023). Can the UKESM and NZESM simulate historical and future SSTs in the South Pacific and beyond well? An evaluation of the model's SSTs is necessary to add.
- Coarse-resolution (100km or less) models usually fail at simulating TC climatology correctly (see Roberts et al. 2020b and numerous other references). The fact that yours would simulate a realistic number of TCs is very surprising, so I would like to see the question of resolution discussed more than it currently is. Simulating cat. 3 TCs in a ~1.5° model more than surprising is worrying, with respect to results by Davis et al. (2018).
- The models' TC climatology is compared to ERA5. Although I understand that the reanalysis is a useful bridge between observations and simulation, all reanalyses, including ERA5 have difficulties in representing TCs, especially the most intense one (see Hodges et al. 2017; Zarzycki et al. 2021; Dulac et al. 2023). These limitations need to be at least acknowledged and discussed. All the more since, in that case, you compare a 30km resolution reanalysis to a 150km resolution model.
- Why not use the observations of TCs in the South Pacific, easily available from IBTrACS, for example? This would provide a more reliable perspective on the figures you provide for the evaluation.
- The paper calls several times to an argument, which is, to my mind, a serious misconception that the trackers would underestimate the number of intense cyclones simulated, which is not based on any reference. Some trackers do underestimate the number of cyclones, but in that case, they miss more likely weak TCs with categories 1 or less. If TCs of category 2 or more are being detected, it is because they are not simulated because the tracker would, with very few exceptions, detect them if they were present in the data. Any underestimation of the number of intense TCs (cat. >= 2) should be attributed to the data and not the tracker.
- Although I was happy at first to see that a validation of the tracking methodology was performed, I was very disappointed by the shallowness of the analysis. I believe that a shorter but more quantitative analysis would benefit the paper.
- I strongly recommend adding statistical tests to challenge the robustness of the highlighted trends in TC frequency.
- The overall structure of the paper and the organization within the sections should be revised to guide the reader through the different analyses and conclusions. I also think some information/analyses are superfluous in their current state :
- The case studies are a nice illustration, but since they are not used to support any generalization, I would move them to the appendix or remove them.
- The simulations which were made to test the sensitivity to some parameters, are described but never really commented on in the remainder of the paper. I recommend either adding a separate analysis as an appendix that can be summarized in the discussion or removing them altogether.
Here is a suggestion for the outline:
- Introduction
- Tracking methodology description and validation
- Simulation data and validation of the ability of the model(s) to simulate SSTs and TCs
- Future trends in (i) frequency and (ii) intensity associated with (iii) changes in the large-scale environment.
- Discussion and conclusion
DETAILED COMMENTS
- Abstract: The hierarchy and order of information in the abstract do not appear suitable to me. I think the details about the difference between the two models are not suitable for an abstract, and the rest of the information should be re-ordered.
- Introduction: Here, the organization of the information is also not optimal. The tracking is mentioned, I think, too early and too much. Without it, the flow of the first half of the introduction is good, moving from examples to impacts to state-of-the-art knowledge about climate change. I would like to see more context about how GCMs simulate tropical cyclones and why choose this approach, and, if possible, more information regarding existing projections of South Pacific TC activity. Tracking, which is an additional source of uncertainty, might be introduced then and before the outline of the paper.
- Line 55: Maybe summarize the controversy rather than refer to Chand et al. (2022), as it seems highly relevant to your study. I want to know more without reading another paper.
- Line 57-58: I do not understand what the mention of the South Atlantic brings to the discussion here.
- Line 65-67: The sentence is unclear; please rephrase.
- In my opinion, the mention of TRACK is superfluous in the intro.
- Section 2:
- Line 75: Using ERA5 as ground truth is a big hypothesis! ERA5 has some severe shortcomings when it comes to simulating TCs, especially their intensity (see Dulac et al. 2023 for a detailed evaluation). Why not use the observations?
- Please provide a complete description of both tracking algorithms and highlight their differences afterwards.
- Regarding the choice of the box where the genesis has to occur, I do not see how the argument about the ocean resolution in that area relates to something relevant for the selection of TCs. Please detail.
- Paragraph 81-88: The word « result » is misused throught the paragraph. Please be more precise regarding what you designate. Is it the output of the trackers, and more precisely the genesis positions, the track density, etc.?
- « The agreement is striking »: that is not obvious to me. Could you match the detected tracks to provide an objective and quantitative ground for that statement?
- The geographical distribution could be more quantitatively assessed with genesis and track density diagnoses.
- Section 3:
- Figure 2: Maybe write the name of each cyclone in the title of the subplots. You wrote « cycle » instead of « cyclone » twice in the caption. Date tags on the observed tracks could help the reader. Pressure unit is lacking, and no description is given of what the contours represent.
- Line 93-94: « Giselle was an ex-tropical cyclone.» : at what point? By definition, it was not its status for its whole lifetime, so you cannot use such a general description.
- Lines 94-95: Same info is repeated about the track of Giselle being depicted in Figure 2.
- Line 96: « processing,» what do you mean ?
- Line 112: Please precise the financial cost. Is it the most costly event of all time and all types considered, or only weather/disaster-related events?
- Section 2&3: I appreciate that validation of the tracking method is given attention in your study. However, I think it is too shallow in its present state: The two tracking algorithms are compared based on a visual analysis of detected genesis points. A more quantitative analysis would strengthen your validation. Using two case studies could have been a nice illustration, but in that case, it is a missed opportunity if no generalization is provided. Moreover, why not compare stormTracking tracks to TempestExtremes tracks for the two case studies?
In terms of paper structure, if you decide to keep the case studies (which, in my opinion, could become an appendix), I think they should be gathered in the same section as section 2, which would be a whole section dedicated to tracking.
- Section 4:
- Line 124, « results » is again misused. Do you mean « simulations »?
- Line 129: « these additionnal components »: which ones?
- I understand how the different sensitivity tests are important. However, I think describing them in the body of the paper is more distracting to the reader than helpful. I would recommend moving their description and analysis to the appendix and briefly mentioning in the body of the text which aspects were tested and what the outcome was.
- Section 5:
- Throughout the section, please be clear about which period is used at each analysis stage.
- Line 158: Here, it would be useful to use the observations to say whether cat. 4-5 TCs are observed in that basin.
- Line 160: I strongly disagree that the underestimated of the cyclones is a limitation of the tracking algorithms. It is a limitation of the datasets, and the trackers only detect what is simulated. Similarly, your statement in lines 173-174 that « TempestExtremes loses higher category systems » is wrong (and not supported by any citation). It is the simulation that does not feature these storms.
- You need to address the resolution issue more than you currently do. Your atmospheric resolution (1.25°x1.875°) is much lower than what is usually considered necessary to simulate TC climatology correctly (0.5° or less). It seems like you still obtain a realistic number of cyclones, and you simulate TCs of cat. 2 & 3, which is very surprising and cannot be dismissed only with what you write in lines 161-163.
- Line 175: « clearer » that what?
- Instead of making a statement about a frequency trend and dismissing it on the grounds of the low number of cyclones, I strongly recommend a proper statistical test to be performed especially since I would expect that the number of TCs you detect in total and in low categories (several hundred) and the availability of several ensemble members for each scenario would, in fact provide robust statistics.
- Figure 4 caption and line 181: What is the "situation"?
- Line 179: What was this expectation based on? Do you have any references supporting this?
- Line 181: Do you extend to the whole globe or the whole southern hemisphere? Please clarify and refrain from using "global" if you only extend to one hemisphere.
- Line 182: In the observations, the South Pacific is far from accounting for 1/3 of the observed TCs, so you need to comment more on this.
- Lines 184-188: This sounds very anecdotal and potentially noisy without a proper statistical analysis.
- Lines 189-191: Once again, intense cyclones being omitted is not a tracking issue. And I agree that ERA5 underestimates these systems (e.g., Zarzycki et al. 2021, Dulac et al. 2023), which is why comparing to the actual observations would be an important addition.
- Figure 6: Why increase the transparency of the tracks with time? I think the Gabrielle cloud cover is superfluous.
- Figure 7: The boxes in Figure (a) are barely visible. Moreover, it seems like the southernmost box does not have the exact longitude boundaries as the tropical one, contrary to what is written. Please add latitude coordinates on the plots. There are too many plots, and they are too small. Maybe consider plotting tracks from the same scenario on the same panel with different colors/markers for different members. Here also, why increase the transparency of the tracks with time? The dots are taking a lot of space and attention, but the « pressure at cyclogenesis — which I don’t see why it is relevant —- is not commented on in the text.
- What period in the future scenarios are you using? From the figures this is 2080-2099, but this should be specified in the text.
- Line 233: The word « global » cannot designate only the Southern Hemisphere.
- Lines 234-238: The absence of cyclones in the South Atlantic alone cannot be used as an argument to say that the model reproduces well the geographical distribution of TCs in the southern hemisphere. You need better and more quantitative diagnoses. To start with: How many cyclones are simulated in each basin, and how does that compare to ERA5 and the observations? You might then plot track or genesis densities rather than overlapping genesis points.
- Figure 9: Same comments as Figure 7.
- Line 243: Figure numbers are confused; the first should be 8(b) and the second 10(d)
- 5.3: Why not compare your historical climatology to that of ERA5? This is a missed opportunity to evaluate the ability of your model to simulate TC-relevant large-scale environments.
- Figures 12&13: Why is data not shown below ~12°S?
- Conclusion:
- I would like to see a discussion of your results in the context of existing knowledge and uncertainty about future TC trends globally and in the South Pacific.
- I would like to see a discussion of the potential limitations of your study. I have already mentioned coupling and resolution, and I think that acknowledging that the use of only one model, or even of model-based evidence only, is an approach prone to biases is important.
Citation: https://doi.org/10.5194/egusphere-2023-1694-RC1 - In its current form, the assessment of the models' ability to simulate tropical cyclones is not convincing. Here are some points of concern:
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RC2: 'Comment on egusphere-2023-1694', Anonymous Referee #2, 26 Mar 2024
The authors are interested in the development of South Pacific tropical cyclone (TC) activity under global-change scenarios. They consider results from two closely related climate models and, due to largely similar projections, present results from one of the models. The projected changes in TC activity are briefly related to environmental factors that are known to impact TC activity, such as SST and vertical wind shear.
Potential future changes in TC activity, in particular on a regional scale, are of high societal importance. Unfortunately, however, I see little merit in the presented manuscript besides the importance of the considered topic. Most severely, the introduction does not introduce scientific questions that the work sets out to address. The authors state (L54): “Some previous studies have found that Southern hemisphere tropical cyclone – TC – frequency is set to reduce as the climate warms yet some have found the opposite …”. It is not discussed, and thus remains unclear, why the current work would help to reconcile or at least improve on the contrasting results of previous studies.
Besides the lack of scientific questions, the main method is scientifically questionable. The resolution of the atmospheric model (approx. 1.5 deg) is not able to resolve the processes that govern TC genesis and intensification. Importantly, TC intensity is misrepresented at this resolution. Why study a feature that we know the model does not adequately represent? We can, of course, count model TCs, but the epistemic uncertainty remains (and is high). What do we learn about our real world in a potential future? Other studies that investigated TC activity in models with similar coarse resolution restrict themselves to analysis of environmental condition and attempt to draw conclusions on TCs based on statistical relationships. While not perfect, this approach at least acknowledges the limitation of the models more explicitly.
Presented analyses in this manuscript are in general shallow. Text that accompanies figures, and thus could be used to build an argument, is often short. The discussion of the potential role of environmental conditions is a vivid example. In that context, a more specific comment: The authors cite the work by McTaggart-Cowan et al. (2015), but seemingly fail to acknowledge a main point of that study: that it is not(!) the absolute SST that matters for TCs, but a bulk-stability metric, i.e., the temperature differences between the sea surface and the upper troposphere, consistent with Emanuel’s potential-intensity theory. Instead, the authors use such an absolute SST value (26.5C) in their work.
Furthermore, analyses are often inconclusive, and the authors themselves refer to their results sometimes as preliminary.
Unfortunately, I have to recommend rejection and do not have specific recommendation how to improve the manuscript.Citation: https://doi.org/10.5194/egusphere-2023-1694-RC2
Status: closed (peer review stopped)
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RC1: 'Comment on egusphere-2023-1694', Anonymous Referee #1, 24 Jan 2024
This paper proposes a tentative analysis of an ensemble of historical and future climate projections with the UKESM and NZESM to identify potential trends in TC-related risk for New Zealand. To do so, they first validate their tracking methodology by comparing it to another similar methodology widespread in the literature. Then, they evaluate the frequency of TCs in the South Pacific basin then their intensity in the simulations. Finally, some perspective is given regarding how the results can be traced back to the simulated large-scale environment.
The purpose of the paper — a regionalized analysis of the future cyclonic activity in the South Pacific and, more particularly, for New Zealand — is an important and valuable endeavor. If they could be trusted, the conclusions in this paper would be meaningful for local adaptation to climate change. However, in its current state, the paper does not provide an analysis that is rigorous enough for any of the conclusions to be trustworthy.
First, most people well acquainted with the literature regarding GCM simulations of tropical cyclones with GCMs would be wary of the TC climatology simulated by any climate model, even more so a coarse-resolution coupled model. Two main limitations need to be overcome: coarse-resolution models are widely known for failing at simulating tropical cyclones (e.g., Roberts et al. 2020b; Camargo et al. 2013; Tory et al. 2013), and sea-surface temperature biases impact the TC climatology (Huang et al. 2021; Sobel et al. 2023). Neither of these limitations is discussed and addressed. Overall, the validation of the historical simulations barely exists. It is based on comparing the simulated TC climatology to that of ERA5 instead of observations. Although it might be acceptable in some contexts, the limitations of ERA5 itself should be acknowledged, and reasons for not using easily available observations should be provided. As such, the paper does not convince me that the model is simulating South Pacific TCs correctly.
Even if the model simulates cyclones correctly, the analyses made by the authors appear too shallow, especially since they lack basic quantitative and statistical foundations. Finally, the paper is not well structured. Only a complete overhaul of the paper and the addition of essential analyses will make it publishable.
MAJOR COMMENTS
- In its current form, the assessment of the models' ability to simulate tropical cyclones is not convincing. Here are some points of concern:
- Coupled models are known to have sea-surface temperature biases that can greatly affect the simulated climatology of tropical cyclones (e.g., Huang et al. 2021; Sobel et al. 2023). Can the UKESM and NZESM simulate historical and future SSTs in the South Pacific and beyond well? An evaluation of the model's SSTs is necessary to add.
- Coarse-resolution (100km or less) models usually fail at simulating TC climatology correctly (see Roberts et al. 2020b and numerous other references). The fact that yours would simulate a realistic number of TCs is very surprising, so I would like to see the question of resolution discussed more than it currently is. Simulating cat. 3 TCs in a ~1.5° model more than surprising is worrying, with respect to results by Davis et al. (2018).
- The models' TC climatology is compared to ERA5. Although I understand that the reanalysis is a useful bridge between observations and simulation, all reanalyses, including ERA5 have difficulties in representing TCs, especially the most intense one (see Hodges et al. 2017; Zarzycki et al. 2021; Dulac et al. 2023). These limitations need to be at least acknowledged and discussed. All the more since, in that case, you compare a 30km resolution reanalysis to a 150km resolution model.
- Why not use the observations of TCs in the South Pacific, easily available from IBTrACS, for example? This would provide a more reliable perspective on the figures you provide for the evaluation.
- The paper calls several times to an argument, which is, to my mind, a serious misconception that the trackers would underestimate the number of intense cyclones simulated, which is not based on any reference. Some trackers do underestimate the number of cyclones, but in that case, they miss more likely weak TCs with categories 1 or less. If TCs of category 2 or more are being detected, it is because they are not simulated because the tracker would, with very few exceptions, detect them if they were present in the data. Any underestimation of the number of intense TCs (cat. >= 2) should be attributed to the data and not the tracker.
- Although I was happy at first to see that a validation of the tracking methodology was performed, I was very disappointed by the shallowness of the analysis. I believe that a shorter but more quantitative analysis would benefit the paper.
- I strongly recommend adding statistical tests to challenge the robustness of the highlighted trends in TC frequency.
- The overall structure of the paper and the organization within the sections should be revised to guide the reader through the different analyses and conclusions. I also think some information/analyses are superfluous in their current state :
- The case studies are a nice illustration, but since they are not used to support any generalization, I would move them to the appendix or remove them.
- The simulations which were made to test the sensitivity to some parameters, are described but never really commented on in the remainder of the paper. I recommend either adding a separate analysis as an appendix that can be summarized in the discussion or removing them altogether.
Here is a suggestion for the outline:
- Introduction
- Tracking methodology description and validation
- Simulation data and validation of the ability of the model(s) to simulate SSTs and TCs
- Future trends in (i) frequency and (ii) intensity associated with (iii) changes in the large-scale environment.
- Discussion and conclusion
DETAILED COMMENTS
- Abstract: The hierarchy and order of information in the abstract do not appear suitable to me. I think the details about the difference between the two models are not suitable for an abstract, and the rest of the information should be re-ordered.
- Introduction: Here, the organization of the information is also not optimal. The tracking is mentioned, I think, too early and too much. Without it, the flow of the first half of the introduction is good, moving from examples to impacts to state-of-the-art knowledge about climate change. I would like to see more context about how GCMs simulate tropical cyclones and why choose this approach, and, if possible, more information regarding existing projections of South Pacific TC activity. Tracking, which is an additional source of uncertainty, might be introduced then and before the outline of the paper.
- Line 55: Maybe summarize the controversy rather than refer to Chand et al. (2022), as it seems highly relevant to your study. I want to know more without reading another paper.
- Line 57-58: I do not understand what the mention of the South Atlantic brings to the discussion here.
- Line 65-67: The sentence is unclear; please rephrase.
- In my opinion, the mention of TRACK is superfluous in the intro.
- Section 2:
- Line 75: Using ERA5 as ground truth is a big hypothesis! ERA5 has some severe shortcomings when it comes to simulating TCs, especially their intensity (see Dulac et al. 2023 for a detailed evaluation). Why not use the observations?
- Please provide a complete description of both tracking algorithms and highlight their differences afterwards.
- Regarding the choice of the box where the genesis has to occur, I do not see how the argument about the ocean resolution in that area relates to something relevant for the selection of TCs. Please detail.
- Paragraph 81-88: The word « result » is misused throught the paragraph. Please be more precise regarding what you designate. Is it the output of the trackers, and more precisely the genesis positions, the track density, etc.?
- « The agreement is striking »: that is not obvious to me. Could you match the detected tracks to provide an objective and quantitative ground for that statement?
- The geographical distribution could be more quantitatively assessed with genesis and track density diagnoses.
- Section 3:
- Figure 2: Maybe write the name of each cyclone in the title of the subplots. You wrote « cycle » instead of « cyclone » twice in the caption. Date tags on the observed tracks could help the reader. Pressure unit is lacking, and no description is given of what the contours represent.
- Line 93-94: « Giselle was an ex-tropical cyclone.» : at what point? By definition, it was not its status for its whole lifetime, so you cannot use such a general description.
- Lines 94-95: Same info is repeated about the track of Giselle being depicted in Figure 2.
- Line 96: « processing,» what do you mean ?
- Line 112: Please precise the financial cost. Is it the most costly event of all time and all types considered, or only weather/disaster-related events?
- Section 2&3: I appreciate that validation of the tracking method is given attention in your study. However, I think it is too shallow in its present state: The two tracking algorithms are compared based on a visual analysis of detected genesis points. A more quantitative analysis would strengthen your validation. Using two case studies could have been a nice illustration, but in that case, it is a missed opportunity if no generalization is provided. Moreover, why not compare stormTracking tracks to TempestExtremes tracks for the two case studies?
In terms of paper structure, if you decide to keep the case studies (which, in my opinion, could become an appendix), I think they should be gathered in the same section as section 2, which would be a whole section dedicated to tracking.
- Section 4:
- Line 124, « results » is again misused. Do you mean « simulations »?
- Line 129: « these additionnal components »: which ones?
- I understand how the different sensitivity tests are important. However, I think describing them in the body of the paper is more distracting to the reader than helpful. I would recommend moving their description and analysis to the appendix and briefly mentioning in the body of the text which aspects were tested and what the outcome was.
- Section 5:
- Throughout the section, please be clear about which period is used at each analysis stage.
- Line 158: Here, it would be useful to use the observations to say whether cat. 4-5 TCs are observed in that basin.
- Line 160: I strongly disagree that the underestimated of the cyclones is a limitation of the tracking algorithms. It is a limitation of the datasets, and the trackers only detect what is simulated. Similarly, your statement in lines 173-174 that « TempestExtremes loses higher category systems » is wrong (and not supported by any citation). It is the simulation that does not feature these storms.
- You need to address the resolution issue more than you currently do. Your atmospheric resolution (1.25°x1.875°) is much lower than what is usually considered necessary to simulate TC climatology correctly (0.5° or less). It seems like you still obtain a realistic number of cyclones, and you simulate TCs of cat. 2 & 3, which is very surprising and cannot be dismissed only with what you write in lines 161-163.
- Line 175: « clearer » that what?
- Instead of making a statement about a frequency trend and dismissing it on the grounds of the low number of cyclones, I strongly recommend a proper statistical test to be performed especially since I would expect that the number of TCs you detect in total and in low categories (several hundred) and the availability of several ensemble members for each scenario would, in fact provide robust statistics.
- Figure 4 caption and line 181: What is the "situation"?
- Line 179: What was this expectation based on? Do you have any references supporting this?
- Line 181: Do you extend to the whole globe or the whole southern hemisphere? Please clarify and refrain from using "global" if you only extend to one hemisphere.
- Line 182: In the observations, the South Pacific is far from accounting for 1/3 of the observed TCs, so you need to comment more on this.
- Lines 184-188: This sounds very anecdotal and potentially noisy without a proper statistical analysis.
- Lines 189-191: Once again, intense cyclones being omitted is not a tracking issue. And I agree that ERA5 underestimates these systems (e.g., Zarzycki et al. 2021, Dulac et al. 2023), which is why comparing to the actual observations would be an important addition.
- Figure 6: Why increase the transparency of the tracks with time? I think the Gabrielle cloud cover is superfluous.
- Figure 7: The boxes in Figure (a) are barely visible. Moreover, it seems like the southernmost box does not have the exact longitude boundaries as the tropical one, contrary to what is written. Please add latitude coordinates on the plots. There are too many plots, and they are too small. Maybe consider plotting tracks from the same scenario on the same panel with different colors/markers for different members. Here also, why increase the transparency of the tracks with time? The dots are taking a lot of space and attention, but the « pressure at cyclogenesis — which I don’t see why it is relevant —- is not commented on in the text.
- What period in the future scenarios are you using? From the figures this is 2080-2099, but this should be specified in the text.
- Line 233: The word « global » cannot designate only the Southern Hemisphere.
- Lines 234-238: The absence of cyclones in the South Atlantic alone cannot be used as an argument to say that the model reproduces well the geographical distribution of TCs in the southern hemisphere. You need better and more quantitative diagnoses. To start with: How many cyclones are simulated in each basin, and how does that compare to ERA5 and the observations? You might then plot track or genesis densities rather than overlapping genesis points.
- Figure 9: Same comments as Figure 7.
- Line 243: Figure numbers are confused; the first should be 8(b) and the second 10(d)
- 5.3: Why not compare your historical climatology to that of ERA5? This is a missed opportunity to evaluate the ability of your model to simulate TC-relevant large-scale environments.
- Figures 12&13: Why is data not shown below ~12°S?
- Conclusion:
- I would like to see a discussion of your results in the context of existing knowledge and uncertainty about future TC trends globally and in the South Pacific.
- I would like to see a discussion of the potential limitations of your study. I have already mentioned coupling and resolution, and I think that acknowledging that the use of only one model, or even of model-based evidence only, is an approach prone to biases is important.
Citation: https://doi.org/10.5194/egusphere-2023-1694-RC1 - In its current form, the assessment of the models' ability to simulate tropical cyclones is not convincing. Here are some points of concern:
-
RC2: 'Comment on egusphere-2023-1694', Anonymous Referee #2, 26 Mar 2024
The authors are interested in the development of South Pacific tropical cyclone (TC) activity under global-change scenarios. They consider results from two closely related climate models and, due to largely similar projections, present results from one of the models. The projected changes in TC activity are briefly related to environmental factors that are known to impact TC activity, such as SST and vertical wind shear.
Potential future changes in TC activity, in particular on a regional scale, are of high societal importance. Unfortunately, however, I see little merit in the presented manuscript besides the importance of the considered topic. Most severely, the introduction does not introduce scientific questions that the work sets out to address. The authors state (L54): “Some previous studies have found that Southern hemisphere tropical cyclone – TC – frequency is set to reduce as the climate warms yet some have found the opposite …”. It is not discussed, and thus remains unclear, why the current work would help to reconcile or at least improve on the contrasting results of previous studies.
Besides the lack of scientific questions, the main method is scientifically questionable. The resolution of the atmospheric model (approx. 1.5 deg) is not able to resolve the processes that govern TC genesis and intensification. Importantly, TC intensity is misrepresented at this resolution. Why study a feature that we know the model does not adequately represent? We can, of course, count model TCs, but the epistemic uncertainty remains (and is high). What do we learn about our real world in a potential future? Other studies that investigated TC activity in models with similar coarse resolution restrict themselves to analysis of environmental condition and attempt to draw conclusions on TCs based on statistical relationships. While not perfect, this approach at least acknowledges the limitation of the models more explicitly.
Presented analyses in this manuscript are in general shallow. Text that accompanies figures, and thus could be used to build an argument, is often short. The discussion of the potential role of environmental conditions is a vivid example. In that context, a more specific comment: The authors cite the work by McTaggart-Cowan et al. (2015), but seemingly fail to acknowledge a main point of that study: that it is not(!) the absolute SST that matters for TCs, but a bulk-stability metric, i.e., the temperature differences between the sea surface and the upper troposphere, consistent with Emanuel’s potential-intensity theory. Instead, the authors use such an absolute SST value (26.5C) in their work.
Furthermore, analyses are often inconclusive, and the authors themselves refer to their results sometimes as preliminary.
Unfortunately, I have to recommend rejection and do not have specific recommendation how to improve the manuscript.Citation: https://doi.org/10.5194/egusphere-2023-1694-RC2
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