the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 08 Feb 2022
The Mediterranean climate change hotspot in the CMIP5 and CMIP6 projections
Francisco Doblas-Reyes
Martin Jury
Raül Marcos
Pierre-Antoine Bretonnière
Margarida Samsó
Download
- Final revised paper (published on 08 Feb 2022)
- Supplement to the final revised paper
- Preprint (discussion started on 30 Jul 2021)
- Supplement to the preprint
Interactive discussion
Status: closed
-
RC1: 'Comment on esd-2021-65', Anonymous Referee #1, 16 Aug 2021
General comments
The Mediterranean region is an important climate change hotspot due to pronounced warming and drying projected under future greenhouse gas emission scenarios. This article analyses and compares output from CMIP5 and the recent CMIP6 over the region. Its results provide a useful update on Mediterranean projections. Several methodological points require some clarification or slight modification, however.
Specific comments
- Abstract. The abstract is too general. You need to be more specific and give detailed numerical results of the study (the same comment also applies to the conclusion – no numerical values…) In the current version, no numerical values (temperature or precipitation changes, with uncertainties) are given even though they are an important outcome of this study (especially the CMIP5/CMIP6 comparison, and the model weighting). Please consider modifying the abstract (and conclusion) to include them (e.g. ll. 11-12 summer precipitation change, ll. 9-10 how much more warming in CMIP6 vs. CMIP5, etc.) Also, some of the wording is quite general, like l. 14 “in some regions” > please specify.
- Methods section. I find it a bit difficult to read. Most of the elements are there but the structure could be improved. For instance, you begin with “all computations were performed with…” But what computations do you perform? They are only introduced later at l. 122. It would be clearer to begin by saying what computations you perform, and then specify all the technical details (regridding, land vs. ocean, etc.) Maybe also consider having a separate sub-section for the weighing approach.
- Weights definition. The paragraph on the calculation of weights is not very clear. How exactly are Di and Sij are calculated? Is Di = sqrt((TAS-DIFF)**2+(TAS-STD)**2+(TAS-TREND)**2+(PSL-DIFF)**2+(PSL-STD)**2)? Appendix B is not very helpful either as it does not contain the equation. Similarly, the definition of Sij is unclear. Showing an equation would be much better. Additionally, in one sentence the diagnostics are said to be “the 20-year PSL and TAS climatologies” and in the next you say that the diagnostics are computed over the 35-year period. Two different time periods are also used for Di and Sij, which is confusing (see also my next comment)
Also, what observational reference do you choose (in DIFF)? The mean calculated over all observation/reanalysis products? - Baseline periods. The fact that you use two different periods is confusing. First, 20 years is a bit short to calculate averages. 30 years is usually preferred. You mention that 20 years of data are heavily influence by inter-annual variability; that is true for trends, but for averages also. The extra 10 years of observations should also be used to assess GCM performance. Since you have to merge the historical and RCP8.5 simulations in CMIP5 to calculate trends for the 1980-2014 period, why not merge them to calculate averages also? The issue with having those two reference periods is that you mix them in the calculation of weights, which is not very consistent.
- Trend significance. It seems that to detect statistical significance the authors are implementing a t-test to determine whether the ensemble-mean average trend (in TAS or PR) is significantly different from zero. But that is not really appropriate. Trend statistical significance should be assessed for each model separately based on its inter-annual variability. The spread in trend values across models is not related to the magnitude of the trends themselves. For instance, there can be a large spread across models (+1,+2,+5,+10°C) but each trend may be statistically significant for the corresponding model (because inter-annual variability is smaller for the +1°C model than for the +10°C model). A better definition of significance in this context might be the fraction of models for which the trend is significant (or, like robustness, to impose that the trend is significant for at least 80% of models) This could change the conclusions for HighResMIP.
- Results. The section is a bit difficult to read. Maybe you could try to structure it a bit more? For instance, in section 3.2 you move from temperature to precipitation back to temperature and precipitation again, switching between scenarios, seasons and periods.
- Discussion. Despite the emphasis on the “hotspot” aspect, the discussion contains no information on the physical mechanisms responsible for the existence of the Mediterranean hotspot. Some literature exists on the topic (e.g., Brogli et al. https://doi.org/10.1175/JCLI-D-18-0431.1, Tuel et al. https://doi.org/10.1175/JCLI-D-20-0429.1) Please consider adding a short discussion on the comparison of the hotspot between CMIP5 and CMIP6, and the links to the known/likely physical mechanisms.
Technical comments
l.1 “increased warming trend” -> maybe “enhanced warming trend”?
l.1 “makes” -> “make”
l.2 “historical and scenario” -> missing “future”?
l.4 “following scenarios RCP2.6, SSP1-2.6, RCP4.5, SSP2-4.5, RCP8.5 and SSP5-8.5” -> I suggest separating the CMIP5 and the CMIP6 scenarios
l.7 “along” -> “over” (and “over” on l. 8 can become “across” or “during”)
l.9 “being CMIP6” -> “CMIP6 being”
l.17 “continental” -> “oceanic” as well. A continental climate is not “humid and mild”.
ll.17-19 This sentence is unclear. Can you please rephrase?
l.24 “global warming mean” -> “global-mean warming”
l.26 add “are” before “projected”
ll.26-28 Unclear what this sentence refers to here…
l.37 “tools” -> you mean GCMs?
l.59 “assumption” -> “criteria”?
l.62 “presented in section 3”
l.69 It is not just PSL that is used to calculate model weights; TAS is used also, correct?
l.79 “mangnitudes”
l.82 “has” -> “have”
l.89 “initial conditions” (no “-“)
l.96 “containing” -> “including”
l.106 “differences in the thermodynamic properties of the surfaces” -> “differences in surface thermodynamic properties”
Figure 1 -> it would be useful to have also the numerical values for the global/latitudinal mean changes
Table 1. -> Please specify in the caption the variables corresponding to the acronyms (TAS, PR, etc.), or specify later at l.104 when the variables are introduced.
l.145 Did you introduce variable M?
l.149 “weight” -> “more weight”?
l.167 “30-45N latitudinal belt mean” -> Why not all land regions? One could argue that to make it a global hotspot one should compare against all other land areas (say of the same size). One issue also is that both the Mediterranean and the 30-45N belt contain many grid points with very small precipitation averages -> potentially large relative changes which may bias the analysis.
Also, you compare to 30-45N values but only over land, right? In that case Figure S3 should not have data over the oceans. For the sake of readers who are not used to land-only values (“global” often means land and ocean), I suggest you specify “global land mean”, e.g., at l.166.
l.176 “projects larger precipitation increases in regions where the hotspot has a negative sign such as the southeast of the domain” -> unclear. Larger increases where the change is negative?
l.179 “larger scale means” -> “global average”
Figure S5: What are OBS? It would be better to show here the values for the different observation/reanalysis products. Or at least their mean and the range across products (maybe that is what is currently shown, and if yes, please specify in the caption) In HighResMIP values the different markers are also a bit too small to see the difference. Make them bigger maybe?
l.206 “for the remaining seasons” -> “for MAM and SON” (or specify in the previous sentence that you look at DJF and JJA).
l.210 “trend” -> “trends”
l.211 “but the PR high-resolution (HR) models trends display outliers in summer” -> “but some of the high-resolution (HR) models exhibit trends outside the CMIP6 range for PR in summer”
Figures 3 and S6: Could you please add horizontal grid lines? Right now it is difficult to look at this figure and see the differences between weighted and unweighted results.
l.220 “under for” -> “under”
l.227 “cannot be drawn”. Still, you could compare the HighResMIP values with those of the corresponding, low-resolution climate model versions.
l.229 delete “respectively”
l.237 Figure S5, not S3
ll.237-238 “Generally, the signal is weak and the inter-model spread is wide for all multi-model ensembles” -> what does this refer to? Precipitation projections only? If yes “weak” is not really appropriate. Mid-to-long term trends in JJA precipitation are large (-15% or below)
ll.240-244 What is the conclusion here? If you constrain model ECS then you will get a smaller spread in projections.
l.248 “Student’s t-test”
l.253 “CMIP6 systematically projects” instead of “keeps projecting”
l.260 “precipitation changes only get more robust and significant with time” -> does this mean that temperature changes don’t get more robust and significant with time?
l.265-267 Please rephrase.
l.267 “concord” -> “agree”
l.272-273 It sounds like you are saying that precipitation both increases and declines in the Balkans.
l.276-277 This sentence comes a bit out of nowhere. Also, what is the 90% range? Please clarify.
l.278 suggest “Weighted projections” to be consistent with section 3.2
l.293 “The mean signal in CMIP6 decrease whereas it increases in CMIP5”
ll.297-298 “Nevertheless, even if the probability of a future extreme-warming decreases, such temperature increases are still considered valid by the weighted ensemble” -> I suggest rephrasing along the lines of “Nevertheless, even though the weighting approach reduces the probability of the most extreme warming values, they remain possible in the weighted ensemble”.
l.304 “Mediterranean”
ll.306-307 suggest rephrasing as “We have shown that average Mediterranean temperature changes were larger than the global-mean average during summer, but close to it during winter, for all scenarios, time periods and model ensembles.”
l.324 “no clear improvement could be seen from the increased resolution” -> did you compare the HighResMIP models with the lower-resolution versions of the same GCMs?
l.330 “The largest source of uncertainty to determine the warming and precipitation change by the mid and long-term periods is the emission scenario.” Where did you show that? Is it true for both TAS and PR?
l.365 “Precipitation weighted projections are not shown in this study as we have no proof that the diagnostics used to assess temperature are relevant to evaluate the models’ precipitation response.” -> you could still weigh models based on their past precipitation trends, no?
Citation: https://doi.org/10.5194/esd-2021-65-RC1 -
AC1: 'Reply on RC1', Josep Cos, 22 Oct 2021
Dear Referee,
Thanks a lot for the thorough revision of our manuscript as the majority of comments will help us improve the content and readability of our work. The most important message we extract from the revision is that the way the methodology and results are written could be improved (comments 1 & 2) and, therefore, we will apply the suggestions. Additionally, as suggested, we will add some discussion regarding the underlying mechanisms of the Mediterranean hotspot.
There are some methodological issues pointed out by the reviewer that arise from the authors not having successfully conveyed the methods in the text. Therefore, we proceed to clarify these issues and they will be kept in mind when re-writing part of the text (italics refer to your comments):
... Additionally, in one sentence the diagnostics are said to be “the 20-year PSL and TAS climatologies” and in the next you say that the diagnostics are computed over the 35-year period. Two different time periods are also used for Di and Sij, which is confusing (see also my next comment) Also, what observational reference do you choose (in DIFF)? The mean calculated over all observation/reanalysis products?
We always use the 35-year period in the diagnostics used to compute Sij and Di. The 20-year periods are used only when showing the projected results. Therefore, the two periods aren’t mixed within the weighting method. What might have caused some confusion is that the periods 2041-2060 and 2081-2100 are used when finding the magnitude of the optimal shape parameter σd (we need to check how the multi-model ensemble reacts to different values of σd to assess if it would cause and under or over-constraint of the future projections).
Baseline periods. The fact that you use two different periods is confusing. First, 20 years is a bit short to calculate averages. 30 years is usually preferred. You mention that 20 years of data are heavily influence by inter-annual variability; that is true for trends, but for averages also. The extra 10 years of observations should also be used to assess GCM performance. Since you have to merge the historical and RCP8.5 simulations in CMIP5 to calculate trends for the 1980-2014 period, why not merge them to calculate averages also? The issue with having those two reference periods is that you mix them in the calculation of weights, which is not very consistent.
The fact that we used 20 year periods to show mean changes is consistent with the work conducted in the IPCC AR6. As answered in the previous point the weighting method, the verification of the models against observations and the display of the future projections are independent things. For the weights we use the 35-year historical period to ensure that the trend is well represented, the same is true for the verification with observations and finally, when showing the future projected changes we follow the IPCC guidelines to display changes against the baseline period.
Discussion. Despite the emphasis on the “hotspot” aspect, the discussion contains no information on the physical mechanisms responsible for the existence of the Mediterranean hotspot. Some literature exists on the topic (e.g., Brogli et al. https://doi.org/10.1175/JCLI-D-18-0431.1, Tuel et al. https://doi.org/10.1175/JCLI-D-20-0429.1) Please consider adding a short discussion on the comparison of the hotspot between CMIP5 and CMIP6, and the links to the known/likely physical mechanisms.
Thanks a lot for the suggestion, we will consider adding information about the mechanisms that drive the hotspot in the revised manuscript’s discussion.
Finally, there are a couple of suggestions/comments where the authors’ points of view differ from the reviewer’s:
Trend significance. It seems that to detect statistical significance the authors are implementing a t-test to determine whether the ensemble-mean average trend (in TAS or PR) is significantly different from zero. But that is not really appropriate. Trend statistical significance should be assessed for each model separately based on its inter-annual variability. The spread in trend values across models is not related to the magnitude of the trends themselves. For instance, there can be a large spread across models (+1,+2,+5,+10°C) but each trend may be statistically significant for the corresponding model (because inter-annual variability is smaller for the +1°C model than for the +10°C model). A better definition of significance in this context might be the fraction of models for which the trend is significant (or, like robustness, to impose that the trend is significant for at least 80% of models) This could change the conclusions for HighResMIP
While this is an interesting approach to compute the statistical significance of the results, we consider that it wouldn’t correspond to the significance of the results as we show them. The results are obtained using the change in the multi-model ensemble mean. To evaluate if the changes are significant we need information about the difference in ensemble distribution between the historical and future periods, not the significance in the changes of single models. Therefore, we compare the ensemble-mean and model spread between the historical and future periods.
- l.167 “30-45N latitudinal belt mean” -> Why not all land regions? One could argue that to make it a global hotspot one should compare against all other land areas (say of the same size). One issue also is that both the Mediterranean and the 30-45N belt contain many grid points with very small precipitation averages -> potentially large relative changes which may bias the analysis.
We tried several options to illustrate the precipitation hotspot. We compared the Mediterranean precipitation to the global precipitation and the precipitation in the 30-45ºN latitudinal belt to reach the same conclusion: the Mediterranean is projected to experience larger changes than the global mean and the regions with the same latitude. This already stands out when looking at the global maps of precipitation change. Using land-only points in the latitudinal belt does not change the conclusions because many land regions in these latitudes experience important precipitation increases (e.g., South Asia).
Citation: https://doi.org/10.5194/esd-2021-65-AC1
-
RC2: 'Comment on esd-2021-65', Anonymous Referee #2, 02 Sep 2021
The authors analyze CMIP5 and CMIP6 projections over the Mediterranean area and compare the projected changes in temperature and precipitation to global mean changes. Model skill is deduced from comparison to observations datasets during the historical period. Ensemble projections are weighted by the aforementioned skill and degree of independence between members. The subject and methodology is of interest to the scientific community. However, the manuscript needs major revisions, including additional calculations or focusing only on temperature before it can be published.
Major remarks:
- Regarding precipitation: The eastern Mediterranean is characterized by almost completely dry summers and precipitation mostly during winter. Therefore, including it in JJA in the precipitation calculation over the whole Mediterranean basin seems to me problematic. This is seen in the verification against observations for (Fig. S5), and in the lack of robustness and significance in changes (Figs.4). I strongly suggest that the authors do their calculations (not only verification, but all the calculations) considering the very significant differences in precipitation between different regions over the Mediterranean basin.
- Model data and observational data: A table with a list of the grid sizes of each data set is required.
- S5, at least the comparison to observations, should be part of the article body and not a supplement. This is part of the heart of the paper: how to quantify the veracity of the simulations and the results seen in this figure are strongly correlated to the remark #1.
- Due to the complexity of the precipitation analysis I would also suggest limiting the manuscript to temperature only, without the need of additional calculations for precipitation as in remark #1. For instance, as stated in lines 365-366 “Precipitation weighted projections are not shown in this study as we have no proof that the diagnostics used to assess temperature are relevant to evaluate the models precipitation response.” Diagnostics should turn clearer by dividing the Mediterranean basin following precipitation climatic characteristics in the different seasons.
Minor remarks:
Abstract:
The sentence: " Results obtained from the model weighting scheme indicate increases in CMIP5 and reductions in CMIP6 warming trends, thereby reducing the distance between both multi-model ensembles." it is not clear what the reference is to the written increases and reductions, and what variable(s) are the authors referring to.
By lines:
38: "while running the same model multiple times under the same experiment samples internal variability (Hawkins and Sutton, 2011)"
using different initial conditions?
55: "to global-mean and large-scale changes" – Not clear
86-88: "The results from CMIP5 and CMIP6 sharing the same 2100 radiative forcing will be displayed together for simplicity, but the reader should always bear in mind that the evolution of GHG concentrations differs between them". – Not clear.
108-113: "The baseline periods 1986-2005 and 1980-2014 are the reference to assess the models performance against observations. The shorter 1986-2005 period (from Collins et al. (2013)) serves as a baseline for the calculation of climate change signals. The longer reference period (35 years) is used to compute historical trends, as 20-year trends are considered to be too heavily influenced by internal variability (Merrifield et al., 2020; Peña-Angulo et al., 2020). The reason for using the older 1986- 2005 20-year period instead of the more recent 1995-2014 (Brunner et al., 2020) is to avoid CMIP5’s historical period ending in 2005 to overlap with the corresponding scenario projection runs that start in 2006"
Not clear. For the historical comparison between CMIP5 and CMIP6 to observations to be statistically consistent to say something about the skill of CMIP5 versus CMIP6 the same period has to be used. From the text and from the periods that these projects are available it seems to me that the comparison against observations is done for different periods. Then we cannot compare between CMIP5 and CMIP6 skills. The text above is not clear. Should it be written separately that 1986-2005 is used for signals and 1980-2014 for performance against observations?
117-119: "The height differences between the model orography and the evaluation grid implies that TAS must be corrected (by means of the 6.49 K/km standard lapse rate) whenever absolute climatologies are used (Weedon et al., 2011; Dennis, 2014)." Not clear
128-129: "A climate change signal is considered robust when at least 80 % of the models agree on the sign of change (Collins et al., 2013)." – Not conditioned to model-observations agreement during the historical period of the aforementioned models?
158-159: "Each multi-model ensemble" – I understood there is one multi-model ensemble, maybe it should be written each “model ensemble”? Or maybe each “member in the multi-model ensemble?
165-168: "Figure 1 compares warming differences of the high radiative forcing scenarios of CMIP5 and CMIP6 over the Mediterranean with respect to the 1986-2005 global mean for winter, summer and the annual means. For precipitation, Mediterranean change is compared to the 30º N-45º N latitudinal belt mean. The Mediterranean region shows a higher annual temperature increase than the global mean." – As written here it is very unclear. What was compared here? My guess is as follows: (a) temperature and precipitation change was calculated globally against 1986-2005, (b) the same as (a) was done only for the Mediterranean region, (c) in the plots we see (b) minus (a). Is this correct? This is not written above.
Fig. 1: Either I missed it or there is no discussion at all about the positive change in precipitation shown in JJA panels of CMIP5 RCP8.5 and CMIP6 SSP5-8.
206: "Mostly, for the remaining seasons,…"- What is not the “remaining season”? It seems a sentence is missing before
Citation: https://doi.org/10.5194/esd-2021-65-RC2 -
AC2: 'Reply on RC2', Josep Cos, 22 Oct 2021
Dear Referee,
The authors want to thank you for your time and the revision of our manuscript. The comments will help us improve the content and robustness of our work. The most important message we extract from the review is that the methods followed to show precipitation projections should be clarified and modified to make our work more consistent.
Nevertheless, the authors have a slightly different point of view regarding some of the comments. Therefore, we would like to take advantage of the discussion period to have a conversation on some of the points (italics refer to your comments):
1. Regarding precipitation: The eastern Mediterranean is characterized by almost completely dry summers and precipitation mostly during winter. Therefore, including it in JJA in the precipitation calculation over the whole Mediterranean basin seems to me problematic. This is seen in the verification against observations for (Fig. S5), and in the lack of robustness and significance in changes (Figs.4). I strongly suggest that the authors do their calculations (not only verification, but all the calculations) considering the very significant differences in precipitation between different regions over the Mediterranean basin.
From our point of view, this shouldn't be an issue as the area aggregations we have applied are computed with the absolute rather than the relative values. Nevertheless, this was not the case for the MedHS scatter plots. We will redo them following your suggestion.
2. S5, at least the comparison to observations, should be part of the article body and not a supplement. This is part of the heart of the paper: how to quantify the veracity of the simulations and the results seen in this figure are strongly correlated to the remark #1.
Thanks for the suggestion, we agree that the comparison to observations should be displayed in the body of the article. We will move the historical trend comparison to the main text.
3. Due to the complexity of the precipitation analysis I would also suggest limiting the manuscript to temperature only, without the need of additional calculations for precipitation as in remark #1. For instance, as stated in lines 365-366 “Precipitation weighted projections are not shown in this study as we have no proof that the diagnostics used to assess temperature are relevant to evaluate the models precipitation response.” Diagnostics should turn clearer by dividing the Mediterranean basin following precipitation climatic characteristics in the different seasons.
From the authors’ understanding of the hotspot, it is important to include the effect of precipitation. Regarding the weighting method and precipitation, it is an issue that is yet to be resolved as diagnostics used to constrain temperature are inadequate for precipitation. We plan to further investigate this issue in the future.
The authors think that splitting the Mediterranean domain escapes the aim of assessing the region as a whole and as defined by the IPCC. Going back to our answer to point 1, the area-averaged relative changes have been aggregated from the single grid-points absolute values, and therefore, results shouldn’t be affected by large relative changes in arid regions.
Citation: https://doi.org/10.5194/esd-2021-65-AC2
-
RC3: 'Comment on esd-2021-65', Anonymous Referee #3, 24 Sep 2021
The manuscript compares regional climate changes in the Mediterranean area between CMIP5 and CMIP6. It is a good complement to the general efforts of the international scientific community exploring the added-value of CMIP6, with its predecessor CMIP5 as a basic reference. The manuscript also includes an attempt to improve the multi-model ensemble-processing methodology by implementing an algorithm considering both models performance and inter-dependence. The manuscript is generally well written and organized in a logic way. I think it can be accepted for publication after a few minor revisions.
1. The manuscript would be of higher value if there are some comparisons with similar works performed in other geographic sectors of the world. For example, there are some recent efforts focusing on regional climate issues in China (Zhu et al. 2020, 2021, Li et al. 2021: https://doi.org/10.1007/s00376-020-9289-1 ; https://doi.org/10.1016/j.scib.2021.07.026 ; https://doi.org/10.1007/s13351-021-0067-5).
2. Although CMIP5’s RCP scenarios are close to CMIP6’s SSP scenarios with the relevant nomenclature, there are indeed subtle differences for greenhouse gases, especially for emission of aerosols. This seems ignored in the present manuscript. In a more general manner, differences between CMIP5 and CMIP6, as analysed in the manuscript, include many aspects involving both anthropogenic emissions and improvement of models’ physics and resolution. It seems that one cannot make a clear idea or conclusion, with what presented in the manuscript.
3. The ensemble-processing algorithm, based on models’ performance and independence, imposes an observation constraint. The authors state that its use can make closer the results of CMIP5 and CMIP6, and make smaller the spreading of each ensemble among its members. They also point out a few exceptions. Are there any explanations? Generally speaking, the manuscript seems a little too descriptive and lacks physical interpretation.
4. It is a little disappointing to see only mean climate (for both surface air temperature and precipitation) is processed here, without consideration of any extreme climate events or their representative indices.
5. Line 165, Figure 1. The figure legend and associated descriptions are confusing for me. “…with respect to the 1986-2005 GLOBAL mean…”; “with respect to the MEAN GLOBAL temperature change and the MEAN 30º N-45º N LATITUDINAL BELT precipitation change”. The authors need to clearly indicate what are particular in the displayed graphics, compared to usual practices.Citation: https://doi.org/10.5194/esd-2021-65-RC3 -
AC3: 'Reply on RC3', Josep Cos, 22 Oct 2021
Dear Referee,
The authors would like to thank you for your time and the revision of our preprint. The suggestions will be of great value to improve the manuscript. The main impression we extract from your comments is that our work is lacking some physical justification of the hotspot and the projections. We will try to take it into account in the revised work by more carefully studying the current knowledge on the drivers of the Mediterranean hotspot and their implications through the different CMIPs.
We would also like to take advantage of this message to discuss specifically some of the comments received (italics refer to your comments):
- The manuscript would be of higher value if there are some comparisons with similar works performed in other geographic sectors of the world. For example, there are some recent efforts focusing on regional climate issues in China (Zhu et al. 2020, 2021, Li et al. 2021: https://doi.org/10.1007/s00376-020-9289-1 ; https://doi.org/10.1016/j.scib.2021.07.026 ; https://doi.org/10.1007/s13351-021-0067-5).
Thanks a lot for the suggestion. We will consider adding such a comparison in the revised manuscript discussion.
- Although CMIP5’s RCP scenarios are close to CMIP6’s SSP scenarios with the relevant nomenclature, there are indeed subtle differences for greenhouse gases, especially for emission of aerosols. This seems ignored in the present manuscript. In a more general manner, differences between CMIP5 and CMIP6, as analysed in the manuscript, include many aspects involving both anthropogenic emissions and improvement of models’ physics and resolution. It seems that one cannot make a clear idea or conclusion, with what presented in the manuscript.
Thanks for letting us know that the manuscript seems to be lacking comments on the differences between RCPs and SSPs. Even if the authors consider that in section 2.1 (l.80) their differences are reviewed, we will try to make it clearer in the new iteration of the manuscript.
Regarding the conclusions that can be extracted from the manuscript in terms of CMIP5 and CMIP6 differences, there is no clear statement that can be drawn without being speculative. Therefore, the authors have based their understanding of the differences between CMIPs on the current literature, such as differences in the cloud feedbacks, aerosol forcings and aerosol-cloud interactions.
- The ensemble-processing algorithm, based on models’ performance and independence, imposes an observation constraint. The authors state that its use can make closer the results of CMIP5 and CMIP6, and make smaller the spreading of each ensemble among its members. They also point out a few exceptions. Are there any explanations? Generally speaking, the manuscript seems a little too descriptive and lacks physical interpretation.
Thanks for pointing this out. The authors agree that further physical interpretation of the outcome of the weights should be conducted.
In the manuscript, we based the justification of the CMIP6 ensemble shifting towards CMIP5 on the emergent constraints work from Nijesse et al. 2020 and Tokarska et al. 2020. Their work states that models with higher climate sensitivity aren’t consistent with the observed global warming trends. We have conducted further tests and found out that this is not a good explanation for our constraining weights obtained in the Mediterranean region. This is displayed in the figures shown below. Figure 1 represents the performance weights (left) and the full weights (right) against their 2081-2100 warmings with respect to 1986-2005 for DJF (a) and JJA (b). It aims to highlight which effect has each weight (independence and performance) on the ensemble distribution shifts.
The differences between the left and right panels highlight how the independence weighting is the one reducing the warming from the CMIP6 ensemble rather than the performance weighting. CMIP6 Performance-only weights shift the ensemble to the high end of changes for JJA while they keep the ensemble quite unchanged for DJF. Contrarily, the addition of independence weighting shifts it to the lower end for both seasons. It can also be seen that the addition of independence weighting doesn't affect the CMIP5 mean state.
Therefore, an interpretation of the weights that shall be included in the revised manuscript is that CMIP6’s distribution is moving towards the CMIP5 ensemble because of the independence weighting effect.
As a final justification of why the simple explanation on the basis of the ECS is not applicable, we display, in Figure 2, the performance (left) and full (right) weights against the model’s ECS for DJF (a) and JJA (b). The figure shows how performance gives weight to models with high ECS in JJA and doesn’t down-weight them in DJF. Therefore we can’t see a clear relationship between low performance and high model’s ECS.
In the revised manuscript we will base the justification of the weighted CMIP6 shift on the causes and effects of independence discrimination.
- It is a little disappointing to see only mean climate (for both surface air temperature and precipitation) is processed here, without consideration of any extreme climate events or their representative indices.
The authors agree that it would be very interesting to assess extreme climate events. Nevertheless, we have considered that the paper is already too dense to add this kind of indices. Thanks for the suggestion, it will definitely be part of our future work.
Nijsse, F. J. M. M., Cox, P. M., and Williamson, M. S.: Emergent constraints on transient climate response (TCR) and equilibrium climate sensitivity (ECS) from historical warming in CMIP5 and CMIP6 models, Earth Syst. Dynam., 11, 737–750, https://doi.org/10.5194/esd-11-737-2020, 2020.
B. Tokarska, M. B. Stolpe, S. Sippel, E. M. Fischer, C. J. Smith, F. Lehner, R. Knutti, Past warming trend constrains future warming in CMIP6 models. Sci. Adv. 6, eaaz9549 (2020).
-
AC3: 'Reply on RC3', Josep Cos, 22 Oct 2021
Peer review completion
