the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
Ubiquity of human-induced changes in climate variability
Keith B. Rodgers
Isla R. Simpson
Malte F. Stuecker
Who M. Kim
Danica L. Lombardozzi
William R. Wieder
Stephen G. Yeager
- Final revised paper (published on 09 Dec 2021)
- Supplement to the final revised paper
- Preprint (discussion started on 06 Jul 2021)
- Supplement to the preprint
CC1: 'Comment on esd-2021-50', Richard Rosen, 11 Jul 2021
AC1: 'Reply on CC1', Keith Rodgers, 03 Sep 2021
We appreciate the comments offered through the public comment on our manuscript. The core suggestion of the reviewer concerns our choice of scenario (SSP3-7.0) and our choice to run our simulations through the year 2100 so as to consider variance changes at the end of the 21st century, rather than choose the near-term years 2040 or 2050. Our decisions in these matters were anchored in community-based decisions as reflected for example in the O’Neill et al. (2016) ScenarioMIP paper, that suggested SSP3-7.0 for large ensemble simulations. And more broadly, we chose to follow in most ways the CMIP6 protocols that were developed through broad community decision-making over the last 5 years. We wish in no way to denigrate or dissuade research focusing on nearer-term changes, nor does our work endorse or “choose” most likely outcomes of political decisions or put our money on the most likely scenario for future change. The O’Neill et al. (2016) study was quite specific in its recommendation that as a relatively strong scenario, SSP3-7.0 offers relatively strong forcing, with this being appropriate for studying changes of variance over the 21st century. We’re sorry for any misunderstandings in this regard. In the revised text, we will state more clearly how our model configuration was chosen within the context of broader CMIP6 efforts.
As a matter of procedure, we would encourage the reviewer to participate in the development of protocols for CMIP7, as this is where the protocols that shape studies such as ours are developed and expressed to the climate community. To reiterate, the interests and questions raised by the reviewer are clearly of value and interest for enhancing both public awareness and policy. But procedurally the most constructive way to bring such concerns to the table may not be through arguing posteriori that submitted manuscripts have illegitimate priorities for their chosen timescales (is any timescale illegitimate in climate science?), but rather in shaping community priorities through open processes.
- AC1: 'Reply on CC1', Keith Rodgers, 03 Sep 2021
RC1: 'Comment on 'Ubiquity of human-induced changes in climate variability' by Rodgers et al.', Anonymous Referee #1, 28 Jul 2021
The manuscript features an evaluation of several key components of the climate system, focusing on statistics of their variability and how they change as a conseguence of anthropogenic climate change. The analysis makes use of the largest (among the recently performed) Large Ensemble (LE) experiment, carried out with CESM2 model. In order to assess changes in the statistics, historical and SSP3-7.0 scenarios are considered, and decadal averages are performed. The authors find that the signature of climate change is apparent, not only in the mean state change, but also in the variance, in the occurrence of extreme events, in the amplitude and frequency of certain periodic oscillations, and in some aspects of co-variability of selected quantities.
Overall, I think that the manuscript is scientifically sound, the methodology is reasonably correct in its implementation, consistently with the aim of exploiting the opportunity given by the huge CESM2-LE dataset to perform an in-depth analysis of climate variability from a global-scale point of view. Nevertheless, I think that the authors miss the chance to provide an interpretation of their findings. As a result, the manuscript is characterized by a collection of outputs loosely connected with each other. Secondarily, a few methodology aspects deserve more careful consideration, such as bringing together runs with different treatment of biomass burning fluxes, selecting the initialisation points according to the phase of the AMOC, or considering 10-year period as a sufficiently long decorrelation timestep for the sampling of initial conditions. Finally, I think that the manuscript would benefit by better referencing the available literature, particularly on the impact anthropogenic climate change has on variance and extremes.
Once these points, that are specifically addressed in the comments below, are taken into account, I think that the mansucript could be accepted for publication.
ll. 33-37: I find a bit limiting the notion of fluctuations as "characterized by spectral variance peaks superimposed upon a broad noise background", as I think it does not entails the possibility that modes of spatio-temporal variability are actually influenced by the "noise background" itself. Especially when one deals with processes that have clearly non-Gaussian PDFs, as in the case of this analysis, it is worth mentioning that at least that multiplicative noise processes (and externally driven changes therein) can alter the modes of variability through nonlinear interaction (e.g. Majda et al. 2009; Sardeshmukh and Sura 2009; Sardeshmukh and Penland 2015);
ll.62-64: while I find that mentioning Milinski et al. 2020 objective algorithm for the detection of the required LE size is appropriate, I think that, being the algorithm model dependent, it shall be acknowledged that their conclusions do not a priori apply here. Possibly, a sampling over the pre-industrial simulation, using it to test the internal variability associated with ENSO, would hint at the number of members that is actually required (even though one would have to assume that the same holds when the SSP3-7.0 forcing is applied).
ll. 106-107: the choice of the section of the pre-industrial run, where the model drift is particularly small, shall be better justified. The internal variability of the model might be influenced by the presence (or absence) of such bias, and it would be relevant to assess how relevant this impact is;
ll. 108-116: I am a bit puzzled by the choice of the initialisation dates for the ensemble. 80 members are initialised with 4 initial dates (sampled according to the phase of the AMOC; maximum AMOC, minimum AMOC, ascending AMOC, descending AMOC), then slightly perturbing these initial conditions (20 members per date); for the additional 20 members, initial dates separated by 10 years were chosen. I find hardly justifiable that the members are to be considered as independent and identically distributed, and that, as such, conclusions can be drawn about ensemble mean moments of the distribution. I acknowledge that, as the authors state at ll. 122-123, "further quantitative exploration of the specific duration over which initial condition memory is retained is the subject of a separate ongoing study" but I see two issues in this choice of the initial dates: 1. Members chosen according to AMOC phase are not uncorrelated by construction; 2. when it comes to the internal variability of the ocean, it is quite unlikely that 10 years are a sufficient decorrelation time;
ll. 130-136: I do not think that enough evidence is here provided that the two ensembles with different biomass burning can be assumed as being (or not being) part of the same population. An assessment through statistical tests (e.g. Mann-Whitney?) would here support such an argument;
ll. 175: out of curiosity, I was wondering why the authors chose to take into account the maximum transport at 40 N, instead of 26.5 N (which is often considered as an AMOC metrics);
ll. 201-202: as the authors refer here to variance and extremes, and their changes in future climate, it might be worth noticing that some promising results have been achieved with methods that synthesize several or all moments of the PDF, e.g the Wasserstein distance (cfr. Ghil 2015; Robin et al. 2017; Vissio et al. 2020 for a climate models diagnostics application);
l. 227: I do not have clear why the authors decided to retain the seasonal cycle in this context;
ll. 246-247: this is one of a few sentences I found in the text, that justify my general comment above about the lack of interpretation. In particular, the authors mention a lead-lag relation between precipitation and SST seasonal maxima. The assessment of these relations are challenging in the context of climate models (e.g. Lembo et al. 2017), together with their interpretation (cfr. Su et al. 2005 for this specific context) and the authors might want to discuss what these mean in terms of dynamics of the system;
l. 276: This is in part already known. Several studies (e.g. Screen 2014, Chen et al. 2015, Haugen et al. 2018) have evidenced the relation between Arctic amplification and reduced temperature variance over the mid- and high-latitudes of the Northern Hemisphere, and an interpretation of this has been given from a dynamical point of view (cfr. Sun et al. 2015; Schneider et al. 2015), involving the role of precipitation;
ll. 322-323: same as in my comment to l. 276. I am not surprised that the authors find a reduction in the NEP inter-annual variability, as this is linked to the variability of near-surface temperature. The link has been discussed in previous works (e.g. Yao et al. 2021) and I believe it shall be taken into account here;
ll. 328-330: see my comment at ll. 246-247. I think the authors shall comment on this finding and on how this can be interpreted;
ll. 350-351: this is not a new achievement. It has been long known (see, e.g. Palmer 1993; Corti et al. 1999) that climate change projects on modes of variability in several ways;
l. 360: I wonder if the authors are able to comment on how significant these findings obtained with CESM2-LE are, in relation with the other Large Ensemble exercices described in Maher et al. 2021;
l. 364-367: the lack of interpretation of the findings is here evident. I don’t think that the take-home message is that the Earth system is “far more sensitive in its statistical characteristics to anthropogenic forcing than previously recognized”. There is actually a literature on assessing changes in higher order moments of several aspects of climate variability, often using Large Ensemble exercises, e.g. Swain et al. 2018, for regional precipitation, Tamarin-Brodsky et al. 2020, for NH temperature variability, among others. The authors might compare their results with others, in order to explain how the sensitivity of statistical characteristics was less recognized before. As mentioned above, some of the findings, taken one by one, are confirming, or possibly expanding, what was already somehow kown from previous works. The manuscript might be significantly improved, if the authors would at least qualitatively discuss what drives and what is the relation between e.g. changes in frequency and phasing of ENSO wrt. SSTs and precipitations, cross-ensemble SD for temperature and precipitation, changes in ENSO’s remote correlation with regional mean temperatures and precipitation over some regions, just to mention a few features that might be interpreted in the light of changes occurring to the general circulation.
- l. 9: replace "runs" with "run";
- l. 150: replace "weaking" with "weakening";
- l. 209: replace "associate" with "association";
- l. 256: replace "n" with "in";
- Chen, H. W., Zhang, F., and Alley, R. B. (2016). The Robustness of Midlatitude Weather Pattern Changes due to Arctic Sea Ice Loss, Journal of Climate, 29(21), 7831-7849
- Corti, S., Molteni, F. and Palmer, T. (1999). Signature of recent climate change in frequencies of natural atmospheric circulation regimes, Nature, 398, 799–802
- Ghil, M., and Lucarini, V. (2020). The physics of climate variability and climate change}, Rev. Mod. Phys., 92 (3), 035002, 77
- Haugen, M. A., Stein, M. L., Moyer, E. J., and Sriver, R. L. (2018). Estimating Changes in Temperature Distributions in a Large Ensemble of Climate Simulations Using Quantile Regression, Journal of Climate, 31(20), 8573-8588
- Lembo, V., Bordi, I., and Speranza, A. (2017). Annual and semiannual cycles of midlatitude near-surface temperature and tropospheric baroclinicity: reanalysis data and AOGCM simulations, Earth Syst. Dynam., 8, 295–312
- Majda, A., Franzke, C. L. E., and Crommelin, D. (2009). Normal forms for reduced stochastic climate models. Proceedings of the National Academy of Sciences of the United States of America, 106, 3649–3653
- Palmer, T. N. (1993). A nonlinear dynamical perspective on climate change, Weather, 48, 313–348
- Sardeshmukh, P. D. and Sura, P. (2009). Reconciling non-Gaussian climate statistics with linear dynamics. Journal Climate, 22(5), 1193–1207
- Sardeshmukh, P. D. and Penland, C. (2015). Understanding the distinctively skewed and heavy tailed character of atmospheric and oceanic probability distributions. Chaos, 25(3), 036410
- Schneider, T., Bischoff, T., and PÅotka, H. (2015). Physics of Changes in Synoptic Midlatitude Temperature Variability, Journal of Climate, 28(6)
- Screen, J. (2014). Arctic amplification decreases temperature variance in northern mid- to high-latitudes. Nature Clim Change 4, 577–582
- Su, H., Neelin, J. D., and Meyerson, J. E. (2005). Mechanisms for Lagged Atmospheric Response to ENSO SST Forcing, Journal of Climate, 18(20), 4195-4215
- Sun, L., Deser, C., and Tomas, R. A. (2015). Mechanisms of Stratospheric and Tropospheric Circulation Response to Projected Arctic Sea Ice Loss, Journal of Climate, 28(19), 7824-7845
AC2: 'Reply on RC1', Keith Rodgers, 03 Sep 2021
We thank the reviewer for their careful reading of the manuscript. In our responses detailed below to the review, we have dedicated our attention wherever possible to the suggestion that we take the opportunity to provide an interpretation of our findings. To this end, we have emphasized in our responses where we plan to anchor the descriptions of our large ensemble behavior to mechanisms and model behaviors identified in previous studies.
Our detailed responses are below. For purposes of clarity, we have put the reviewer comments/questions in italicized text, and responded in plain text.
ll 33-37: I find a bit limiting the notion of fluctuations as “characterized by spectral variance peaks superimposed upon a broad noise background”, as I think it does not entail the possibility that modes of spatio-temporal variability are in fact influenced by the “noise background” itself. Especially when one deals with processes that have clearly non-Gaussian PDFs, as in the case of this analysis, it is worth mentioning that at least multiplicative noise processes (and externally-driven changes therein) can alter the modes of variability through nonlinear interaction (e.g. Majda et al, 2009; Sardeshmukh and Sura, 2009; Sardeshmukh and Penland, 2015).
We thank the reviewer for raising this point. Indeed the role of multiplicative noise in affecting variability on a multitude of timescales is well established in the literature. The references suggested by the reviewer will be included in the revised draft, in addition to references to Levine and Jin (2010; JAS) and Jin et al. (2020, Simple ENSO Models in AGU monograph on El Niño in a changing climate). To our knowledge the Mueller paper is the first that describes the influence of multiplicative noise on second- and third-order cumulants and spectra in the context of the stochastic climate model. The other papers touch on the highlight the role of multiplicative noise in generating ENSO characteristics.
We will further revise the text by adding the following sentence: “The spectrum of observed regional-to-global climate fluctuations exhibits spectral variance peaks and a broad noise background (Hasselmann, 1976; Franzke et al., 2020). Spectral peaks can emerge from a range of mechanisms, including astronomical forcings and internal climate instabilities, such as for ENSO. Moreover, these distinct features can be further influenced by climate processes acting on different timescales. Examples for this type of nonlinear “timescale interaction” are multiplicative (state-dependent) noise (Mueller, 1987; Majda et al., 2009; Sardeshmukh and Sura, 2009; Sardeshmukh and Penland, 2015; Jin et al., 2007; Levine et al., 2010; An et al., 2020; Jin et al., 2020) and combination model dynamics (Stuecker et al., 2015).
ll 62-64: while I find that mentioning Milinski et al. (2020) objective algorithm for the detection of the required LE size is appropriate, I think that with the algorithm being model-dependent, it should be acknowledge that their conclusions do not a priori apply here. Possibly a sampling over the pre-industrial simulation, using it to test the internal variability associated with ENSO, would hint at the number of members that is actually required (even though one would have to assume that the same holds when the SSP3-7.0 forcing is applied).
The point of the reviewer regarding the model-dependence of the Milinski et al. (2020) study is well-taken, and this question is the subject of an independent study with CESM2 led by one of our coauthors, Tamas Bodai. It is indeed not possible to project the necessary ensemble size in a model based on findings from another model configuration, and there are other issues that complicate the idea of prescribing a general rule ensemble sizes required for an experiment. As for the generic idea of an ensemble-size dependence o f detectability and the accuracy of identifying forced changes, the following figure considers variance changes for Niño3 SST following the suggestion of the reviewer:
In the figure, rho denotes the detection rate, calculated with a bootstrap mean over 1e3 bootstrap samples, and F refers to the F-test for the slope, concerning whether it is significantly non-zero at the 95% significance level. HAC refers to a technique that considers heterscedasticity and auto-correlation – which are themselves in fact not detectable here, hence the agreement between rho_F and rho_F,HAC . Thus the 20th century changes in the model are already detectable with 20 ensemble members.
The study of Milinski (2020) is not concerned with detectability, but rather with the accuracy of large changes, and this is addressed by the yellow and purple lines in the figure. alpha is the temporal slope of the ensemble standard deviation, and the purple line indicates the best estimate from the 100 ensemble members. q97.5 and are the 97.5th quantile (corresponding to the upper (u) bound of the 95% confidence interval) and the standard deviation over the bootstrap samples, respectively, with the relative errors/”variance” plotted.
ll. 106-107: the choice of the section of the pre-industrial run, where the model drift is particularly small, should be better justified. The internal variability of the model might be influenced by the presence (or absence) of such bias, and it would be relevant to assess how relevant this impact is.
In the revised manuscript, we will provide a clearer description of model drift over the span of the initialization dates from the pre-industrial control run. In the CESM2 presentation paper of Danabagoglu et al. (2020), Fig 6. Showed the TOA energy imbalance for the pre-industrial run over years 1-1200, revealing minimal drift by year 1000. Additional extensive diagnostics by NCAR scientists identified minimal drift for the AMOC, and for upper ocean heat content over the North Atlantic and Southern Ocean over years 1000-1300.
ll 108-116: I am a bit puzzled by the choice of the initialization dates for the ensemble. 80 members are initialized with 4 initial dates (sampled according to the phase of the AMOC; maximum AMOC, minimum AMOC, ascending AMOC, descending AMOC), then slightly perturbing these initial conditions (20 members per date); for the additional 20 members, initial dates separated by 10 years were chosen. I find hardly justifiable that the members are to be considered as independent, and identically distributed, and that as such, conclusions can be drawn about ensemble mean moments of the distribution. I acknowledge that, as the authors state at ll. 122-123, “further quantitative exploration of the specific duration over which initial condition memory is retained is the subject of a separate ongoing study”, but I see two issues in this choice of the initial dates: 1. Members chosen according to AMOC phase are not uncorrelated by construction; 2. When it comes to the internal variability of the ocean, it is quite unlikely that 10 years are a sufficient decorrelation time.
We were not sufficiently clear in our submitted manuscript about issues surrounding the initialization strategy, through a mix of macro-and micro-perturbations. It was not our intention to argue that the initialization procedure for CESM2-LE produces members that can be considered as independent, and we should have stated this more clearly, we apologize for the misunderstanding. Our analysis with internal variability is primarily focused on the post-1960 period, so more than a century after the 1850 initialization time for all members. In order to clear up any potential confusion, in addition to more detailed text clarifying the initialization procedure, we will provide in the revised manuscript both a quantification of the decorrelation timescale for the AMOC, as well as a timeseries figure showing the evolution of AMOC transport over the late 19th century for the 4 sets of micro-perturbation runs, illustrating the timescale over which initial condition memory is lost.
It is always hard to know how to review articles like this which depend on large groups of climate models which relatively few experts in such models begin to understand. Thus rather than focus on the methodological details of the research which most readers will not understand anyway, it might make the most sense for the authors to focus on the implications of the results for policy makers and other interested readers. The first few sections should be shortened, and the end discussion should be greatly expanded so that policy makers are led through a clear discussion of what the results imply for real problems such as sustainable agriculture that the world faces.
One methodological problem I find in many articles which utilize very high forcing results for a scenario such as 7 watts per square meter like this one does is that by 2100 the temperature increases implied alone might imply the destruction of major parts of the world and human civilization. Thus, this is a very unlikely scenario to occur, especially since policy makers are now focusing on keeping the maximum average global temperature increase to between 1.5 and 2.0 degrees Cby 2050 or 2060, not 4.5 degrees C by 2100 as in this scenario.
Therefore, I think this kind of analysis would make much more sense if it were done for a scenario which achieved net zero carbon emissions by 2060 at the latest, in order to show policy makers why the world should try to achieve net zero carbon emissions even sooner given the implications of this kind of large ensemble modeling effort for the year 2060. Ignore the year 2100 in a revised paper - it is not relevant. Policy makers and the general public need to focus on analytical results for modeling efforts like this paper attempts over a much shorter time frame. The authors might even want to focus on the negative implications of this kind of frequency analysis on years even earlier, such as 2040 and 2050, if that could be done in a scientifically convincing way. If that is done in a revised paper in a convincing way it might get a large readership. It would be important to describe in detail what about the findings are really new in a revised paper. Given the too long run focus of the current paper, it is basically irrelevant for climate change mitigaion policy development, and should not be published as is.