the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
10 Feb 2021
10 Feb 2021
On structural errors in emergent constraints
- 1CERFACS, Toulouse, France
- 2Cornell University, Ithaca, NY, USA
- 3National Center for Atmospheric Research, Boulder, CO, USA
- 4Lawrence Berkeley National Lab, CA, USA
- 5LMD/IPSL, Sorbonne Université, Paris, France
- 6UK Met Office, Exeter, UK
- 7ETH Zurich, Switzerland
- 1CERFACS, Toulouse, France
- 2Cornell University, Ithaca, NY, USA
- 3National Center for Atmospheric Research, Boulder, CO, USA
- 4Lawrence Berkeley National Lab, CA, USA
- 5LMD/IPSL, Sorbonne Université, Paris, France
- 6UK Met Office, Exeter, UK
- 7ETH Zurich, Switzerland
Abstract. Studies of emergent constraints
have frequently proposed that a single metric alone can constrain future responses of the Earth system to anthropogenic emissions. The prevalence of this thinking has led to literature and messaging which is sometimes confusing to policymakers, with a series of studies over the last decade making confident, yet contradictory, claims on the probability bounds of key climate variables. Here, we illustrate that emergent constraints are more likely to occur where the variance across an ensemble of climate models of both observable and future climate arises from common structural assumptions and few degrees of freedom. Such cases are likely to occur when processes are represented in a common, oversimplified fashion throughout the ensemble, about which we have the least confidence in performance out of sample. We consider these issues in the context of a number of published constraints, and argue that the application of emergent constraints alone to estimate uncertainties in unknown climate responses can potentially lead to bias and overconfidence in constrained projections. Together with statistical robustness and plausibility of mechanism, assessments of climate responses must include multiple lines of evidence to identify biases that arise from common oversimplified modeling assumptions which impact both present and future climate simulations in order to mitigate against the influence of common structural biases.
Benjamin M. Sanderson et al.
Status: final response (author comments only)
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RC1: 'Comment on esd-2020-85', Anonymous Referee #1, 10 Mar 2021
The authors have assessed the application of emergent constraints to estimate uncertainties in unknown climate projections. The recent increase in the application of emergent constraints in Earth Science makes this a timely issue, even more in the last year since the new ensemble of Earth system models (CMIP6) became available. Furthermore, the manuscript is very well written and structured, which made it a pleasure to read. However, the main motivation for the paper is that emergent constraints are used too literally (line 681) and “confusing to policymakers” (line 17). I do not fully share this assumption and I argue below why I think this is not the case. Overall, I have major and minor questions that would need to be resolved before a possible publication.
Major comments:
1) The manuscript reads more like a review and less like a research article. The analysis in this paper includes (a) calculating correlations between different published variables, (b) a bootstrapping approach to exploit previously published emergent constraints, and (c) the exploitation of two differential equations with a random number generator to create many ensemble members.
Taken together, I cannot see how this would be a sufficiently novel concept, idea, tool, or data given that was not previously exploited.
Point (b) somehow tests the robustness of the linear relationship. What is the advantage of this method compared to the published measures of uncertainty (e.g. prediction intervals, see minor comment 1). Already the published results of all shown ECS are not different within their still relatively large uncertainties (Table 4 in Schlund et al. (2020)). So, I am wondering what additional information is obtained by performing this bootstrapping.
Point (c) seems to be a more of a fancy way of saying that the Earth System responds at different timescales and not just one, a well-known concept and used to calculate the temperature response to radiative forcing changes (Stocker et al., 2013; Otto et al., 2015). It is therefore obvious that the 2-timescale model continues to heat although radiative forcing stabilizes, and the 1-timescale model does not.
Taken these results together, I do not see a (novel) advance here although the Discussion and presentation of the results is very well done. Overall a lot of times ‘may’ and ‘might’ are used indicating that this is more speculative. However, I hope that the authors can convince me that I am wrong. If not, I would propose to make it a review or perspective paper.
2) Many points that are discussed here as shortcomings of emergent constraints should, in my opinion, be attributed to the models themselves. Emergent constraints can, by definition, only improve the model output. If the models have structural shortcomings, they exist in the multi-model mean and the constrained results. Emergent constraints can thus ‘only’ improve the existing model output and cannot go further. The exchangability argument (lines 66-76, lines 296-304, lines 412-420) is thus wrongly stated in my opinion.
An emergent constraint can only say: models that tend to simulate a large (small) variable A at present (e.g. extent of the Hadley Cell) also simulate a large (small) increase in variable B. If, and only if, a mechanistic relationship can be given and proven to a sufficient level, one could conclude that if models had rightly (as in the observations) simulated variable A, the model result for variable B would be the following.
The constraint can never overcome model shortcomings or biases that exist across the entire model ensemble and is not designed to do that. The exchangability argument would thus only hold if the constrained result would be considered the truth, which it is obviously not. It is just an improved projection, but still based on imperfect models.
As an example, the present temperature and the leaf area index are within the current model ensemble good predictors of future GPP (Schlund et al., 2020). By using the present-day temperature and the leaf index, one can thus show how a model of the same ensemble would likely simulate future GPP if it had the right temperature and leaf index. Nevertheless, if the whole ensemble would be systematically biased and missing out an important process, like nitrogen limitation (lines 296-304), the emergent constraint cannot assess this. The systematic bias is present in the multi-model mean results and the constraint results and thus not primarily an issue of the constrained but the model ensemble. However, it is equally important to mention and assess these uncertainties when presenting mutli-model means and constrained results.
Overall, I think the exchangability argument is wrongly stated as the models in an emergent constraint were never meant to be exchangeable, but observations are only used to inform the likely best guess of a given model ensemble. Having said this, the question remains how systematic model biases should be accounted for in uncertainty range. When calculating the multi-model mean, the standard deviation is often a measure of uncertainty, but this is not taking into account biases or structural errors. So, one can argue that the given uncertainties for a constrained result are equivalent to the uncertainties calculated by the multi-model standard deviation.
Lines 412-420 make the point very clear. The current knowledge of the Earth System is as good as possible implemented in the Earth system models. Some processes known to be missing or wrongly represented, others are probably missing but not known yet (like the ocean mixing in the 1-timescale model). However, these missing processes are strictly speaking a problem of the models. If we had no knowledge of the ocean’s importance (1-timescale model) and only lambda would be of importance, we had implemented no ocean in our models. Thus, the relationship would resemble the red points in figure 2e,f with model lambdas being different because of different atmospheric model components. By applying the hypothetically ‘observed’ lambda, we would reduce uncertainties related to the atmospheric model. We would, however, not find the right results because all models are missing the ocean component. Nevertheless, given the assumed hypothetical current state of knowledge (ocean is not important), and the consequent hypothetical models (no ocean), our knowledge of lambda and the emergent constraint would still ‘improve’ model projections under this assumption. Following this argument in its strict sense, would lead to the conclusion that models cannot be used because important steps might be missing and NOT that emergent constraints cannot be used. The ‘assessment of underlying model assumptions’ (line 436) should always be done if model output of any type is published, constrained or not constrained.
If I understand the conclusion in lines 676-678 right, the authors argue that CMIP models are a comprehensive representation of the Earth System. Following that line of argument, we should not use them either to make projections of climate change at all? Or under which conditions?
3) The manuscripts title, abstract, Conclusion (and partly Introduction) suggests that emergent constraints across the field of Earth Science are addressed. However, throughout the manuscript it becomes clear that the focus of the manuscript is on emergent constraints of the Equilibrium Climate Sensitivity. In addition, other constraints, such as for the Transient Climate Response and the land carbon cycle, are (briefly) discussed. However, constraints for the ocean, a major part of the Earth System, are not discussed at all. Thus, the title and abstract are highly misleading.
I would suggest to either clearly indicate that the manuscript is on emergent constraints on ECS and only discuss ECS constraints or add examples of ocean constraints and largely expand their exposition in section 5.
Examples for emergent constraints in oceanography would be: Kessler et al. (2016), Kiwatkowski et al. (2017), Goris et al. (2018), Terhaar et al. (2020a), Terhaar et al. (2020b). The list is very likely not sufficient.
Furthermore, the ocean is ignored in questions about the ECS or atmospheric CO2 (point 6), although the 2 timescale models clearly indicate that the ocean is important.
4) I am not a statistician, but I have strong concerns regarding the application of statistics in this study. First, I disagree that the Sherwood “D” and Cox constraints are correlated (Line 141). A r (if it is r) of 0.31 is a r2 of less than 0.1. A p-value is not given but I do not expect it to be supportive of a correlation. Even for Lipat and Qu, the r2 is ‘only’ 0.33. Please do not use the term correlated if the variables are not statistically correlated. Second, the two constrained ECS do not disagree (Line 142). Sherwood et al. (2014) find an ECS likely at 4°C with 3°C as a lower limit. Cox et al. (2018) report 2.8 ± 0.6 °C. Within the uncertainty ranges, they agree with each other. Lipat et al. (2018) and Qu et al. (2014) do not even give a constrained result for ECS as far as I can see this. But for this argument we can use the Schlund et al. (2020) estimate for the EC from Lipat et al., which is 3.0 ± 0.8 °C and try to read the result for Qu et a. (2014) from the corresponding subpanel, leading to 3.5 ± 0.4°C. These two constrains do also agree.
The following paragraph paragraph and conclusions are thus wrong.
5) The authors often use the argument that emergent constraints might be confusing to policy makers or other people. Furthermore, they say speak about their ‘literal interpretation (line 196). I can see no evidence supporting this claim. On the contrary most emergent constraints only give a ‘likely’ estimate (summarized in table 4 in Schlund et al. (2020)) and even if all ECSs were used to give a best estimate with an uncertainty range, all ECS would agree. Thus, these ECS seem to be used to exclude outliers and not give a narrowly constrained result. Given that they all agree, I do not see the possible confusion.
6) Lines 442-446: The authors claim that the differences in atmospheric CO2 are caused by the land carbon sink, whereas Hoffmann et al. (2014) clearly state that “Weak ocean carbon uptake in many ESMs contributed to this bias, based on comparisons with observations of ocean and atmospheric anthropogenic carbon inventories.” While the land carbon sink is very uncertain, the ocean has been found by Hoffmann et al (2014) to cause the bias. Please correct your paragraph accordingly. I would also argue that the bias-persistence in the too small ocean carbon sink (Kessler et al. (2016), Goris et al. (2018)) is caused by the circulation differences and is persistent over large timescales and thus not overconfident. The whole section should hence be replaced.
Minor comments:
1) Figure 1: The panels are too small and impossible to read, especially on the diagonal. I suggest keeping y and x labels with the name of the constraint only at the left column and the bottom line. Furthermore, I cannot understand the added value from the bootstrapping algorithm from the manuscript. Often the uncertainty of the fit is estimated by prediction intervals (Bracegirdle et al. 2012; Nijsse et al. 2020; …). To which degree and why does the bootstrap method improve the results, or the estimated uncertainties compared to these prediction intervals. If no improvement exist, why would you not just show the published results (Schlund et al. 2020)? And if you recompute them, why not showing the mean estimate + uncertainties + r2 or something similar. At the moment the subpanels do not allow to assess the mean, the uncertainty or anything else because they are too small.
2) Line 102: Table 3 is mentioned in the text before table 2.
3) Is the bootstrap approach general knowledge? If not, please consider telling the reader how it works or give a reference.
4) Lines 114-121: This is very hard to read, and I am not sure that I understand the message. Could you try to rephrase it and make sure that the reader understands when a combination is appropriate and when not and why?
5) In general: How do you define correlation (Pearson's product-moment coefficient r or something else?)
6) Lines 206 to 209: I do not agree with this statement. Let’s assume variable A (present) is correlated to variable B (projection) across a model ensemble and the correlation is mechanistically profound and supported by theory and observations. If variable A is now a very complex interplay of many processes, it could have a large inter-model spread without a lack of diversity. Thus, the presence of an EC can be a lack of diversity or a complex interplay of different processes. The sentence now is rather misleading.
7) Lines 227-230: You should include Kessler et al (2016) and Goris et al. (2018) here.
8) Lines 250-267: You should add Terhaar et al. (2020a,b) here, although it is not strictly a feedback process but identifying the leading order process that describes the future response.
9) Lines 269-285: You should add Kwiatkowski et al. (2017) here.
10) Line 288-290: I again do not agree with this sentence. A set of models with very complicated assumptions in different processes that govern both related variables, variable A (observable) and variable B (projected), would lead to a large spread in A and B and possible to a good correlation and EC.
11) Equations are not numbered
12) Equation on line 341 is difficult to read (latex problem?)
13) Lines 492-499: What is the added information here? It sounds more speculative than informative.
14) Section 5.3: Your two timescale models are constructed to make just this point. Maybe you could use this here and emphasize hence the importance of the ocean for long-scale warming (ECS) and point out that the difference in the ocean may, according to your model, be responsible for the different long-term temperature trajectories.
15) Lines 537-644: I do not see from which results this conclusion is drawn. Could you pleas just point me to it? And what other metrics are you referring to here?
16) Lines 554-660: Please cite here the multi-variable approach by Schlund et al. (2020)
References
Bracegirdle, T. J., & Stephenson, D. B. (2012). On the robustness of emergent constraints used in multimodel climate change projections of Arctic warming. Journal of Climate, 26(2), 669-678.
Brient, F. (2020). Reducing uncertainties in climate projections with emergent constraints: Concepts, examples and prospects. Advances in Atmospheric Sciences, 37(1), 1-15.
Cox, P. M., Huntingford, C., & Williamson, M. S. (2018). Emergent constraint on equilibrium climate sensitivity from global temperature variability. Nature, 553(7688), 319-322.
Eyring, V., Cox, P. M., Flato, G. M., Gleckler, P. J., Abramowitz, G., Caldwell, P., ... & Williamson, M. S. (2019). Taking climate model evaluation to the next level. Nature Climate Change, 9(2), 102-110.
Goris, N., Tjiputra, J. F., Olsen, A., Schwinger, J., Lauvset, S. K., & Jeansson, E. (2018). Constraining projection-based estimates of the future North Atlantic carbon uptake. Journal of Climate, 31(10), 3959-3978.
Hall, A., Cox, P., Huntingford, C., & Klein, S. (2019). Progressing emergent constraints on future climate change. Nature Climate Change, 9(4), 269-278.
Hoffman, F. M., Randerson, J. T., Arora, V. K., Bao, Q., Cadule, P., Ji, D., ... & Wu, T. (2014). Causes and implications of persistent atmospheric carbon dioxide biases in Earth System Models. Journal of Geophysical Research: Biogeosciences, 119(2), 141-162.
Kessler, A., & Tjiputra, J. (2016). The Southern Ocean as a constraint to reduce uncertainty in future ocean carbon sinks. Earth System Dynamics, 7(2), 295-312.
Kwiatkowski, L., Bopp, L., Aumont, O., Ciais, P., Cox, P. M., Laufkötter, C., ... & Séférian, R. (2017). Emergent constraints on projections of declining primary production in the tropical oceans. Nature Climate Change, 7(5), 355-358.
Lipat, B. R., Tselioudis, G., Grise, K. M., & Polvani, L. M. (2017). CMIP5 models' shortwave cloud radiative response and climate sensitivity linked to the climatological Hadley cell extent. Geophysical research letters, 44(11), 5739-5748.
Nijsse, F. J., Cox, P. M., & Williamson, M. S. (2020). Emergent constraints on transient climate response (TCR) and equilibrium climate sensitivity (ECS) from historical warming in CMIP5 and CMIP6 models. Earth System Dynamics, 11(3), 737-750.
Otto, F. E., Frame, D. J., Otto, A., & Allen, M. R. (2015). Embracing uncertainty in climate change policy. Nature Climate Change, 5(10), 917-920.
Schlund, M., Lauer, A., Gentine, P., Sherwood, S. C., & Eyring, V. (2020a). Emergent constraints on equilibrium climate sensitivity in CMIP5: do they hold for CMIP6?. Earth System Dynamics, 11(4), 1233-1258.
Schlund, M., Eyring, V., CampsâValls, G., Friedlingstein, P., Gentine, P., & Reichstein, M. (2020b). Constraining uncertainty in projected gross primary production with machine learning. Journal of Geophysical Research: Biogeosciences, 125(11), e2019JG005619.
Sherwood, S. C., Bony, S., & Dufresne, J. L. (2014). Spread in model climate sensitivity traced to atmospheric convective mixing. Nature, 505(7481), 37-42.
Stocker, T. (Ed.). (2013). Climate change 2013: the physical science basis: Working Group I contribution to the Fifth assessment report of the Intergovernmental Panel on Climate Change. Cambridge university press.
Terhaar, J., Kwiatkowski, L., & Bopp, L. (2020a). Emergent constraint on Arctic Ocean acidification in the twenty-first century. Nature, 582(7812), 379-383.
Terhaar, J., Torres, O., Bourgeois, T., & Kwiatkowski, L. (2020b). Arctic Ocean acidification over the 21 st century co-driven by anthropogenic carbon increases and freshening in the CMIP6 model ensemble. Biogeosciences Discussions, 1-30.
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AC1: 'Reply on RC1', Ben Sanderson, 30 Apr 2021
Many thanks to the reviewer for taking the time to assess the paper - we will respond to comments in line. Following the comments of this review and others, we have restructured the paper as a review article
The authors have assessed the application of emergent constraints to estimate uncertainties in unknown climate projections. The recent increase in the application of emergent constraints in Earth Science makes this a timely issue, even more in the last year since the new ensemble of Earth system models (CMIP6) became available. Furthermore, the manuscript is very well written and structured, which made it a pleasure to read.
Thanks the kind comments and thoughtful review.
However, the main motivation for the paper is that emergent constraints are used too literally (line 681) and “confusing to policymakers” (line 17). I do not fully share this assumption and I argue below why I think this is not the case.
We argue below why we find this position to be justified.
Major comments:(1) The manuscript reads more like a review and less like a research article. The analysis in this paper includes (a) calculating correlations between different published variables, (b) a bootstrapping approach to exploit previously published emergent constraints, and (c) the exploitation of two differential equations with a random number generator to create many ensemble members. Taken together, I cannot see how this would be a sufficiently novel concept, idea, tool, or data given that was not previously exploited. Point (b) somehow tests the robustness of the linear relationship. What is the advantage of this method compared to the published measures of uncertainty (e.g. prediction intervals, see minor comment 1). Already the published results of all shown ECS are not different within their still relatively large uncertainties (Table 4 in Schlund et al. (2020)). So, I am wondering what additional information is obtained by performing this bootstrapping. Point (c) seems to be a more of a fancy way of saying that the Earth System responds at different timescales and not just one, a well-known concept and used to calculate the temperature response to radiative forcing changes (Stocker et al., 2013; Otto et al., 2015). It is therefore obvious that the 2-timescale model continues to heat although radiative forcing stabilizes, and the 1-timescale model does not. Taken these results together, I do not see a (novel) advance here although the Discussion and presentation of the results is very well done. Overall a lot of times ‘may’ and ‘might’ are used indicating that this is more speculative. However, I hope that the authors can convince me that I am wrong. If not, I would propose to make it a review or perspective paper.
Thanks for this point. We, in fact, fully agree that the analytical aspects of this paper do not represent sufficient quantitative advances in the understanding of combining constraints, and are rather intended to illustrate the wider conceptual points which are the focus of the paper (which the reviewer clearly appreciates, given the comments which follow). Given this (and similar assessments from the other reviewers), we have requested for the paper to be be classed as a review. In this context, we have removed the bootstrapping analysis - given the point has been largely covered by Caldwell 2018, Schlund 2020 and Brient 2019.
We see the paper's novelty as a conceptual framework to assess how emergent constraints relate to model assumptions. Given this, the toy model analysis does not provide deep insight on the nature of ocean timescale response, nor was it intended to. The point illustrates that if a model ensemble contains common approximations and a small number of degrees of freedom (in this case, represented by a single layer ocean), then strong emergent constraints can emerge which would confidently constrain the future response to a certain value - but the constraint may be broken, or simply not exist if a more complex model with additional degrees of freedom is used (here illustrated by a 2 layer ocean). The actual models used are incidental - they simply illustrate models at two different complexity levels. We go in in the discussion section to consider cases where such common oversimplifications may exist in the CMIP class models (e.g. soil respiration-temperature relationships).
Many points that are discussed here as shortcomings of emergent constraints should, in my opinion, be attributed to the models themselves. Emergent constraints can, by definition, only improve the model output. If the models have structural shortcomings,
they exist in the multi-model mean and the constrained results. Emergent constraints can thus ‘only’ improve the existing model output and cannot go further.We broadly agree that the key issue at hand is the structural shortcomings of the models. However, we disagree that the ECs can 'only improve' existing model output - because of the implied precision in the value of the true future response which arises from considering only the error implicit in the regression relationship. An emergent constraint, literally, proposes that an unknown quantity is constrained, unlike an ensemble multi-model mean which just a model estimate with no pretense of precision. Thus, the precision of the EC can potentially be over-stated through the lack of consideration of aspects of common, oversimplified structural assumptions which create strong ensemble relationships. As such, although the structural errors are ultimately features of the models themselves, the use of ensemble relationships which are themselves subject to model errors impacts directly on the 'added value' of emergent constraints.
The exchangability argument (lines 66-76, lines 296-304, lines 412-420) is thus wrongly stated in my opinion. An emergent constraint can only say: models that tend to simulate a large (small) variable A at present (e.g. extent of the Hadley Cell) also simulate a large (small) increase in variable B. If, and only if, a mechanistic relationship can be given and proven to a sufficient level, one could conclude that if models had rightly (as in the observations) simulated variable A, the model result for variable B would be the following. The constraint can never overcome model shortcomings or biases that exist across the entire model ensemble and is not designed to do that. The exchangability argument would thus only hold if the constrained result would be considered the truth, which it is obviously not. It is just an improved projection, but still based on imperfect models.This point is well taken, but contains an implicit assumption that the use of an emergent constraint can \emph{only improve} a projection - where we would argue that ECs have the potential to make an overconfident projection due to a consideration of only the subset of available model validation data which was used in the EC. Fundamentally - the structural errors have the capacity not just to impact the simulated values of A and B, but also the the relationship between A and B - perhaps creating relationships which would not be present in a superset of models. We have already seen that different emergent constraints can emerge from the same ensemble with differing conclusions (e.g. the fluctuation dissipation relationship of Cox et al 2019, and the atmospheric stability relationship of Sherwood 2015). Either of these constraints used alone would constrain ECS to low or high values respectively. These problems are not insurmountable - the Bayesian framework of Williamson 2019 allow for the combination of different lines of evidence, but enacting such a strategy requires the modeling community to engage with (1) the independence of different constraints (e.g. Caldwell 2018) but also (2) the degree to which common structural errors could bias A, B or the relationship between them.
Our position is thus not that the constraints have no value, rather that the common assumption that a constraint used in isolation to constrain a projected ensemble distribution is not justified without considering other relevant aspects of model performance (including other ECs) and the realism of potential common structural assumptions which may have biased or created the emergent relationship. As we argue in our conclusions - we believe that there is a middle ground between standalone emergent constraints, and generic model multi-variate skill scores which could allow a focus on variables which might be of relevance to projected climate without relying exclusively on a single relationship.
As an example, the present temperature and the leaf area index are within the current model ensemble good predictors of future GPP (Schlund et al., 2020). By using the present-day temperature and the leaf index, one can thus show how a model of the same ensemble would likely simulate future GPP if it had the right temperature and leaf index.
Nevertheless, if the whole ensemble would be systematically biased and missing out an important process, like nitrogen limitation (lines 296-304), the emergent constraint cannot assess this. The systematic bias is present in the multi-model mean results and the constraint results and thus not primarily an issue of the constraint but the model ensemble. However, it is equally important to mention and assess these uncertainties when presenting mutli-model means and constrained results.
We agree that the structural biases will impact the unconstrained model projection distribution, including the multi-model mean. But there are two further points to consider: (1) the multi-model mean and model distribution is not advertised as a calibrated estimate of a specific value, together with an implicit error and (2) the added value of the emergent constraint is also potentially subject to structural error.
The reviewer's example considers one example of structural error (the omission of N fertilization), and indeed - this is a case where the structural omission may create an over-confident constrained result if used to calibrate future GPP projections (if present day LAI simulation is a function of N-fertilization). We would argue that this is more problematic for the EC than the multi-model mean. Using the EC to calibrate future GPP is explicitly calibrating GPP to compensate for a missing process. This is an additional source of error because the effect of the bias of the missing process may be different for present day and future GPP, and therefore the constrained result stands to be confident, yet wrong.
The use of a single metric therefore throws away any information which is not in the constraint itself. In the reviewer's example, a model tuned to have the right temperature and LAI may be subject to other biases (in present day GPP or latent heat flux, for example), which would have been considered by the developers calibrating the model. As such, the ensemble distribution of projections and ensemble mean result are of course also subject to biases from missing process, but the models are expert tuned considering a wide range of metrics and therefore, to some degree more robust. The use of the EC to calibrate projections effectively allocates zero weight to any orthogonal aspects of model performance (some of which may themselves be emergent constraints on the same quantity in the ensemble).
To put it in Bayesian terms, the prior ensemble distribution is subject to structural errors, but so are the relationships which provide the basis for the emergent constraint. Therefore, the ECs have the potential to be additionally impacted by structural errors than the unconstrained model distribution.
Overall, I think the exchangability argument is wrongly stated as the models in an emergent constraint were never meant to be exchangeable, but observations are only used to inform the likely best guess of a given model ensemble. Having said this, the question remains how systematic model biases should be accounted for in uncertainty range. When calculating the multi-model mean, the standard deviation is often a measure of uncertainty, but this is not taking into account biases or structural errors. So, one can argue that the given uncertainties for a constrained result are equivalent to the uncertainties calculated by the multi-model standard deviation.We agree with the reviewer that the models were not intended to be exchangeable with reality. Model developers are generally keenly aware of the approximations made in their parameterizations. However, we maintain that the exchangeability assumption is implicit in the use of an emergent constraint to estimate the most likely value and uncertainty in that value. This is the view shared by Williamson (2019).
This problem does not apply to the simple estimate of mean and variance of the original model ensemble projections - which may be biased due to missing processes, but they are not, themselves, uncertainty estimates in a projected quantity. ECs, however, frequently use the error in the regression relationship to estimate an uncertainty in the projected quantity (see Cox 2018, Varney 2019 amongst many other examples) - and this additional step is a strong assumption, that the relationship is equally applicable to reality as it is to the models in the ensemble. We have expanded on this point when first introducing the concept of exchangeability in the introduction (line 94).
Lines 412-420 make the point very clear. The current knowledge of the Earth System is as good as possible implemented in the Earth system models. Some processes known to be missing or wrongly represented, others are probably missing but not known yet (like the ocean mixing in the 1-timescale model).
However, these missing processes are strictly speaking a problem of the models. If we had no knowledge of the ocean’s importance (1-timescale model) and only lambda would be of importance, we had implemented no ocean in our models. Thus, the relationship would resemble the red points in figure 2e,f with model lambdas being different because of different atmospheric model components. By applying the hypothetically ‘observed’ lambda, we would reduce uncertainties related to the atmospheric model. We would, however, not find the right results because all models are missing the ocean component. Nevertheless, given the assumed hypothetical current state of knowledge (ocean is not important), and the consequent hypothetical models (no ocean), our knowledge of lambda and the emergent constraint would still ‘improve’ model projections under this assumption.Agreed, this broadly represents our intended illustration with the simple model - that the 'improvement' in this case would give a confident, but ultimately incorrect, constraint on the future dynamics of the model.
Following this argument in its strict sense, would lead to the conclusion that models cannot be used because important steps might be missing and NOT that emergent constraints cannot be used. The ‘assessment of underlying model assumptions’ (line 436) should always be done if model output of any type is published, constrained or not constrained. If I understand the conclusion in lines 676-678 right, the authors argue that CMIP models are a comprehensive representation of the Earth System. Following that line of argument, we should not use them either to make projections of climate change at all? Or under which conditions?
Here we differ from the reviewer. The single layer ocean is useful for some applications. It can capture some of the first order dynamics of the climate system given appropriate parameters. But the nature of that calibration matters. The Emergent Constraint approach takes an extreme position - that only one aspect of the model should be used in tuning (that which is correlated with the future response). This results in a very tight constraint on the single layer model's parameter space, but because the relationship itself is biased by the structural errors in the model - the constrained value is incorrect.
A more robust calibration strategy is to use all available relevant data to calibrate the model (e.g. the entire historical timeseries, paleoclimate records etc). In this case, individual aspects of the model error would still be subject to structural deficiencies, but trade-offs between tuning to different observations would reduce the degree to which the parameters are constrained (see Sanderson 2008 for an example of this in ESMs).
In short, we agree with the reviewer that all model outputs are subject to structural error. But we argue that the sole reliance on projection calibration from a single ensemble relationship in ECs introduces a particularly acute exposure to specific aspects of model error which will invariably lead to overconfident constrained projections.
3) The manuscripts title, abstract, Conclusion (and partly Introduction) suggests that emergent constraints across the field of Earth Science are addressed. However, throughout the manuscript it becomes clear that the focus of the manuscript is on emergent constraints of the Equilibrium Climate Sensitivity. In addition, other constraints, such as for the Transient Climate Response and the land carbon cycle, are (briefly) discussed. However, constraints for the ocean, a major part of the Earth System, are not discussed at all. Thus, the title and abstract are highly misleading. I would suggest to either clearly indicate that the manuscript is on emergent constraints on ECS and only discuss ECS constraints or add examples of ocean constraints and largely expand their exposition in section 5. Examples for emergent constraints in oceanography would be: Kessler et al. (2016), Kiwatkowski et al. (2017), Goris et al. (2018), Terhaar et al. (2020a), Terhaar et al. (2020b). The list is very likely not sufficient.
This is a fair point. Our objective is certainly to talk about the methodology of emergent constraints in general - the key conceptual arguments are not specifically associated with climate sensitivity. We do not seek to exhaustively review or list every published emergent constraint here (this has been done elsewhere, e.g. in Brient 2020, Hall 2019 or Williamson 2018). But - the reviewer is correct that an ocean-specific example would be desirable to illustrate relevant structural assumptions for different broad genres of constraint. We have added a new section 5.3 on constraints on future ocean carbon uptake. Many thanks for the references.
Furthermore, the ocean is ignored in questions about the ECS or atmospheric CO$_2$ (point 6), although the 2 timescale models clearly indicate that the ocean is important.
Point well taken. We have revised the case studies to include ocean processes at relevant points.
4) I am not a statistician, but I have strong concerns regarding the application of statistics in this study. First, I disagree that the Sherwood “D” and Cox constraints are correlated (Line 141). A r (if it is r) of 0.31 is a r2 of less than 0.1. A p-value is not given but I do
not expect it to be supportive of a correlation. Even for Lipat and Qu, the r2 is ‘only’ 0.33. Please do not use the term correlated if the variables are not statistically correlated.Second, the two constrained ECS do not disagree (Line 142). Sherwood et al. (2014) find an ECS likely at 4°C with 3°C as a lower limit. Cox et al. (2018) report 2.8 ± 0.6 °C. Within the uncertainty ranges, they agree with each other. Lipat et al. (2018) and Qu et al. (2014) do not even give a constrained result for ECS as far as I can see this. But for this argument we can use the Schlund et al. (2020) estimate for the EC from Lipat et al., which is 3.0 ± 0.8 °C and try to read the result for Qu et a. (2014) from the corresponding subpanel, leading to 3.5 ± 0.4°C. These two constrains do also agree. The following paragraph paragraph and conclusions are thus wrong.
The revised paper has removed this section entirely - given the paper was already long, and the assessment of EC correlation has been well discussed by Caldwell (2018)
5) The authors often use the argument that emergent constraints might be confusing to policy makers or other people. Furthermore, they say speak about their ‘literal interpretation (line 196). I can see no evidence supporting this claim. On the contrary
most emergent constraints only give a ‘likely’ estimate (summarized in table 4 in Schlund et al. (2020)) and even if all ECSs were used to give a best estimate with an uncertainty range, all ECS would agree. Thus, these ECS seem to be used to exclude outliers and not
give a narrowly constrained result. Given that they all agree, I do not see the possible confusion.Thanks for this point. We have removed the specific references to climate policymaking. We would counter, however, that the majority of emergent constraints use probabilistic language in their primary conclusions - but in almost all cases, these probabilities exclude the potential for errors which are the focus of this study (that is, the uncertainty arising from model common simplifications which project onto either simulated quantities or intra-ensemble relationships).
6) Lines 442-446: The authors claim that the differences in atmospheric CO$_2$ are caused by the land carbon sink, whereas Hoffmann et al. (2014) clearly state that “Weak ocean carbon uptake in many ESMs contributed to this bias, based on comparisons with observations of ocean and atmospheric anthropogenic carbon inventories.” While the land carbon sink is very uncertain, the ocean has been found by Hoffmann et al (2014) to cause the bias. Please correct your paragraph accordingly.
Totally agreed. We apologise for the land-centric discussion and have updated the paragraph accordingly.
I would also argue that the bias-persistence in the too small ocean carbon sink (Kessler et al. (2016), Goris et al. (2018)) is caused by the circulation differences and is persistent over large timescales and thus not overconfident. The whole section should hence be replaced.
We agree with the reviewer that ocean circulation biases play a significant role. However, we disagree that this is the sole source of uncertainty in atmospheric CO2 concentration biases. As we discuss in the revised section - this is a trade-off between numerous factors: ocean productivity, circulation, land carbon and concentration feedbacks and soil temperature response. Systematic common biases in any of these aspects would qualify as a potential structural uncertainty in future CO2 concentrations.
Minor comments:
1) Figure 1: The panels are too small and impossible to read, especially on the diagonal. I suggest keeping y and x labels with the name of the constraint only at the left column and the bottom line. Furthermore, I cannot understand the added value from the bootstrapping algorithm from the manuscript. Often the uncertainty of the fit is estimated by prediction intervals (Bracegirdle et al. 2012; Nijsse et al. 2020; ...). To which degree and why does the bootstrap method improve the results, or the estimated uncertainties compared to these prediction intervals. If no improvement exist, why would you not just show the published results (Schlund et al. 2020)? And if you recompute them, why not showing the mean estimate + uncertainties + r2 or something similar. At the moment the subpanels do not allow to assess the mean, the uncertainty or anything else because they are too small.
We have removed this figure in the revised version.
2) Line 102: Table 3 is mentioned in the text before table 2.
Table 1,3 now removed. Labelling fixed.
3) Is the bootstrap approach general knowledge? If not, please consider telling the reader how it works or give a reference.
Analysis removed in revision.
4) Lines 114-121: This is very hard to read, and I am not sure that I understand the message. Could you try to rephrase it and make sure that the reader understands when a combination is appropriate and when not and why?
This section has been removed in revision
5) In general: How do you define correlation (Pearson's product-moment coefficient or something else?)
This section has been removed in revision
6) Lines 206 to 209: I do not agree with this statement. Let’s assume variable A (present) is correlated to variable B (projection) across a model ensemble and the correlation is mechanistically profound and supported by theory and observations. If variable A is now a very complex interplay of many processes, it could have a large inter-model spread without a lack of diversity. Thus, the presence of an EC can be a lack of diversity or a complex interplay of different processes. The sentence now is rather misleading.
Agreed. and again, this section has now been removed.
7) Lines 227-230: You should include Kessler et al (2016) and Goris et al. (2018) here.
Thanks - agreed. Added.
8) Lines 250-267: You should add Terhaar et al. (2020a,b) here, although it is not strictly a feedback process but identifying the leading order process that describes the futureresponse.
Thanks - we agree that these are process-based constraints, we've removed the word "feedback" from the title to allow a broader definition.
9) Lines 269-285: You should add Kwiatkowski et al. (2017) here.
Agreed, thanks.
10) Line 288-290: I again do not agree with this sentence. A set of models with very
complicated assumptions in different processes that govern both related variables,
variable A (observable) and variable B (projected), would lead to a large spread in A and B
and possible to a good correlation and EC.We disagree with this. If there are a small number of parameters governing a process in similar parameterisation schemes throughout the ensemble - the response of such models to both historical and future forcings will be a function of that small set of parameters, increasing the chance that an emergent relationship might be found.
Soil respiration/temperature relationships are a good example in CMIP, as we point out in the following paragraph. A simple temperature dependency equation has good skill in representing soil respiration in CMIP as a function of temperatures (Todd-Brown et al. 2013), and this enables strong emergent constraints on future soil respiration temperature sensitivity such as Varney (2020). But - this simple temperature relationship also fails to represent a large fraction of spatial variability in observed soil respiration (Todd-Brown et al. 2013) - which is potentially attributable to the common over-simplicity of the representation of the process in the ensemble.
Adding complexity in this case may indeed increase variance in the predictor or predictand, but the increased number of degrees of freedom in the process representation has the potential to add noise to the relationship between the two. However, if the ensemble diversity can be demonstrably reduced to a single process equation with (in the extreme case) one free parameter - responses to different forcings will be correlated by construction.
11) Equations are not numbered}
Fixed
12) Equation on line 341 is difficult to read (latex problem?)
Thanks, fixed
13) Lines 492-499: What is the added information here? It sounds more speculative than informative.We've deleted this paragraph.
14) Section 5.3: Your two timescale models are constructed to make just this point. Maybe you could use this here and emphasize hence the importance of the ocean for long-scale warming (ECS) and point out that the difference in the ocean may, according to your model, be responsible for the different long-term temperature trajectories.
Thanks for this suggestion - we've incorporated this discussion as suggested.
15) Lines 537-644: I do not see from which results this conclusion is drawn. Could you pleas just point me to it? And what other metrics are you referring to here?
We've deleted this paragraph - as the core of the argument is more clearly repeated in the following paragraph.
16) Lines 554-660: Please cite here the multi-variable approach by Schlund et al. (2020)
Thanks - yes. There's also a valid point from this paper on the significance of constraints persisting for multiple generations.
References
Williamson, D. B., & Sansom, P. G. (2019). How are emergent constraints quantifying uncertainty and what do they leave behind?. Bulletin of the American Meteorological Society, 100(12), 2571-2588.
Varney, R. M., Chadburn, S. E., Friedlingstein, P., Burke, E. J., Koven, C. D., Hugelius, G., & Cox, P. M. (2020). A spatial emergent constraint on the sensitivity of soil carbon turnover to global warming. Nature communications, 11(1), 1-8.
Cox, Peter M., Chris Huntingford, and Mark S. Williamson. "Emergent constraint on equilibrium climate sensitivity from global temperature variability." Nature 553.7688 (2018): 319-322.
Sanderson, B. M., Knutti, R., Aina, T., Christensen, C., Faull, N., Frame, D. J., ... & Allen, M. R. (2008). Constraints on model response to greenhouse gas forcing and the role of subgrid-scale processes. Journal of Climate, 21(11), 2384-2400.
Brient, Florent. "Reducing uncertainties in climate projections with emergent constraints: Concepts, examples and prospects." Advances in Atmospheric Sciences 37, no. 1 (2020): 1-15.
Todd-Brown, K. E. O., Randerson, J. T., Post, W. M., Hoffman, F. M., Tarnocai, C., Schuur, E. A. G., & Allison, S. D. (2013). Causes of variation in soil carbon simulations from CMIP5 Earth system models and comparison with observations. Biogeosciences, 10(3), 1717-1736.
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AC1: 'Reply on RC1', Ben Sanderson, 30 Apr 2021
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RC2: 'Comment on esd-2020-85', Anonymous Referee #2, 15 Mar 2021
General Comments
Sanderson et al provide discuss the nature of emergent constraints (ECs), particularly the potential role of structural errors in driving uncertaints in ECs. Overall, I found it difficult to know what to do with this paper. While the material is clearly presented and interesting to read, it feels more like a review article or a perspective, rather than a journal article. The discussion is generally qualitative and/or speculative, and I'm still not quite sure what the main takeaways are. The quantitative analysis in the paper is limited to Figure 1, which shows the relationships between a number of previously published ECs, and Figure 2, which uses the simple energy balance models to illustrate different kinds of ECs identified in the paper. The former has been covered in more detail in papers led by Caldwell, Bretherton and Schlund, while the 2-layer energy balance model has been extensively discussed by Geoffroy et al, Armour, and Lutsko & Popp (some of these papers are cited in the present manuscript). Without more novelty or substance, it is difficult to recommend publication, although I enjoyed reading the manuscript.Moving forward, the authors might want to think of ways to deepen their analysis. One approach might be to develop a mathematical framework or procedure for identifying and speaking about structural errors in emergent constraints. Alternatively, they could focus in on a particular kind of emergent constraint and probe the structural assumptions used by this kind of emergent constraint in more depth. For example, they could dig into the cloud schemes responsible for the process-based constraints on ECS (e.g., the Sherwood, Brient and Zhai constraints) to really understand the underlying structures. A template could be the recent paper by Thackeray et al, which investigates the snow albedo feedback over multiple generations of climate models, including its relationship to the well established emergent constraint on the feedback.
References:
Armour KC (2017) Energy budget constraints on climate sensitivity in light of inconstant climate feedbacks, Nature Climate Change, 7, 331-335
Bretherton, C. and Caldwell, P.: Combining Emergent Constraints for Climate Sensitivity, Journal of Climate, 33(17), 7413–7430. 2020
Caldwell, P. M., Bretherton, C. S., Zelinka, M. D., Klein, S. A., Santer, B. D. and Sanderson, B. M.: Statistical significance of climate sensitivity predictors obtained by data mining, Geophysical Research Letters, 41(5), 1803–1808, doi:10.1002/2014gl059205, 2014.
Caldwell, P. M., Zelinka, M. D. and Klein, S. A.: Evaluating Emergent Constraints on Equilibrium Climate Sensitivity, Journal of Climate, 31(10), 3921–3942. 2018
Geoffroy, O., Saint-Martin, D., Olivié, D. J. L., Voldoire, A., Bellon, G. and Tytéca, S.: Transient Climate Response in a Two-Layer Energy-Balance Model. Part I: Analytical Solution and Parameter Calibration Using CMIP5 AOGCM Experiments, J. Clim., 26(6), 1841–1857, 2013a.
Geoffroy, O., Saint-Martin, D., Bellon, G., Voldoire, A., Olivié, D. J. L. and Tytéca, S.: Transient Climate Response in a Two-Layer Energy-Balance Model. Part II: Representation of the Efficacy of Deep-Ocean Heat Uptake and Validation for CMIP5 AOGCMs, Journal of Climate, 26(6), 1859–1876. 2013b.
Lutsko, N. J., & Popp, M. (2019). Probing the sources of uncertainty in transient warming on different timescales. Geophysical Research Letters, 46, 11367– 11377
Schlund, M., Lauer, A., Gentine, P., Sherwood S. C. and Eyring, V. (2020) Emergent constraints on equilibrium climate sensitivity in CMIP5: do they hold for CMIP6? Earth Syst. Dynam., 11, 1233–1258.
Thackeray, C. W., Qu, X., & Hall, A. (2018). Why do models produce spread in snow albedo feedback? Geophysical Research Letters, 45, 6223– 6231.Technical Corrections:
-The title is vague: "On Structural Errors in Emergent Constraints", and again makes it hard to know what the main takeways are.
-In the first sentence of the introduction, I'm not sure it's right to state that higher CO2 concentrations are a "boundary condition which has yet to be realized". Increasing CO2 concentrations doesn't enter the boundary conditions, it adds a forcing term. So I would describe climate forecasting as an initial value problem, rather than a boundary condition problem.
-The paper claims that the Cox and Sherwood D constraints are well correlated with each other. But in fact the correlation co-efficient is only 0.31 (~10% of the variance explained).
-Typo at L610: "wider constrained range wider"
-L654: In terms of multi-metric approches, the authors may wish to cite the "cloud-controlling factor" approach (see Klein et al for a recent review) which has recently shown promise for constraining cloud feedbacks.References:
Klein S.A., Hall A., Norris J.R., Pincus R. (2017) Low-Cloud Feedbacks from Cloud-Controlling Factors: A Review. In: Pincus R., Winker D., Bony S., Stevens B. (eds) Shallow Clouds, Water Vapor, Circulation, and Climate Sensitivity. Space Sciences Series of ISSI, vol 65. Springer, Cham.-
AC2: 'Reply on RC2', Ben Sanderson, 30 Apr 2021
Sanderson et al provide discuss the nature of emergent constraints (ECs), particularly the potential role of structural errors in driving uncertaints in ECs. Overall, I found it difficult to know what to do with this paper. While the material is clearly presented and interesting to read, it feels more like a review article or a perspective, rather than a journal article. The discussion is generally qualitative and/or speculative, and I'm still not quite sure what the main takeaways are.
Thanks to the reviewer for the feedback on the manuscript. The opinion that the paper is better categorised as a review or perspective was shared by the other reviewers, and the paper is now classed as a review by the journal (and we are framing it as such).
This paper was never intended to be a quantitative analysis - rather as a perspective on the application of emergent constraints found in an ensemble of model simulations where we know there exist structural limitations to models which are represented in model simulations.
Our takeaways are that we demonstrate in a simple model ensembles how structural errors can produce overconfident emergent constraints, introduce a classification scheme for emergent constraints, and discuss a large number of case studies on where structural limitations in current models may be an additional source of error in published constraints.Furthermore, we would argue that this general qualitative discussion is necessary in the literature before specific quantitative advances can be made. The nature of structural errors, by definition, is processes which are not resolved or incorrectly resolved in the model. As such, a quantitative analysis of such errors is not necessarily feasible, but this does not mean that this source of error can be completely disregarded when considering constrained distributions of projected climate quantities produced through consideration of ensemble derived correlations - as is the case in the majority of EC studies published to date.
The quantitative analysis in the paper is limited to Figure 1, which shows the relationships between a number of previously published ECs ... covered in more detail in papers led by Caldwell, Bretherton and Schlund
Given the classification of the paper as a review, we have removed Figure 1 entirely - which originally served to illustrate inter-constraint relationships, but we agree that this topic is adequately covered by Caldwell, Bretherton and Schlund.
Figure 2, which uses the simple energy balance models to illustrate different kinds of ECs identified in the paper. The 2-layer energy balance model has been extensively discussed by Geoffroy et al, Armour, and Lutsko & Popp (some of these papers are cited in the present manuscript).
We agree that Geoffroy, Armour and Lutsko have produced fine papers illustrating the dynamical assumptions of simple energy balance models, but they do not make the point we are making here - that an overly simple model structure can produce very strong emergent constraints which can be demonstrated to be overconfident in the context of information provided by a more complex class of models.
Without more novelty or substance, it is difficult to recommend publication, although I enjoyed reading the manuscript.
We hope our arguments here persuade the reviewer of the novelty of the article - and the need for a non-quantitative discussion on this topic. We hope further that the restructuring of the manuscript as a review will better reflect the article's purpose.
Moving forward, the authors might want to think of ways to deepen their analysis. One approach might be to develop a mathematical framework or procedure for identifying and speaking about structural errors in emergent constraints.
We believe this paper has already been written, by Williamson (2019) - which motivated us to write the present study. Williamson (2019) demonstrated how structural errors could theoretically be implemented in regression-based constraints in a Bayesian statistical model, but did not discuss any concrete case studies of what such structural errors would look like, In this study, we highlight potential sources of structural error and potential paths forward to future approaches which could better represent these errors in constraints.
Alternatively, they could focus in on a particular kind of emergent constraint and probe the structural assumptions used by this kind of emergent constraint in more depth. For example, they could dig into the cloud schemes responsible for the process-based constraints on ECS (e.g., the Sherwood, Brient and Zhai constraints) to really understand the underlying structures. A template could be the recent paper by Thackeray et al, which investigates the snow albedo feedback over multiple generations of climate models, including its relationship to the well established emergent constraint on the feedback.
Papers focusing on the structural assumptions in individual constraints are enormously valuable, and our section 5 discusses a large number of case studies and how sources of structural error might arise. However, to objectively quantify these errors for any of the studies referenced would be a study in itself, and is far beyond the scope of this article.
In conclusion, we see the necessity for a general article on the potential for structural errors in emergent constraints, rather than a deep dive into a specific process, because there is a general lack of discussion of such errors in papers published to date - with a near blanket assumption that relationships found between predictors and predictands in the multi-model ensemble can be used to reduce uncertainty in projected quantities. In the study, we have demonstrated a simple model case where this assumption is demonstrably false, and we have highlighted where relevant structural assumptions may exist in the current model archive. We hope, in turn, that this will provoke future study which will work towards building constraints which are more robust to structural errors.
Technical Corrections:-The title is vague: "On Structural Errors in Emergent Constraints", and again makes it hard to know what the main takeaways are.
Revised to "On the potential for structural errors in emergent constraints" - which well captures our topic.
In the first sentence of the introduction, I'm not sure it's right to state that higher CO2 concentrations are a "boundary condition which has yet to be realized". Increasing CO2 concentrations doesn't enter the boundary conditions, it adds a forcing term. So I would describe climate forecasting as an initial value problem, rather than a boundary condition problem.
We have changed "boundary conditions" to "forcings" to remove this ambiguity.
More generally - we agree, that if humans are considered part of the Earth System, then it could be argued that climate projections are an initial condition problem (with boundary conditions being only variations in solar forcing). However, it is generally accepted in the climate literature that the initial conditions refer only to the state of physical climate system at the time of initialization (see, e.g. Hawkins and Sutton 2009, Deser 2012, Hawkins 2016, Sriver 2015).
-The paper claims that the Cox and Sherwood D constraints are well correlated with each other. But in fact the correlation co-efficient is only 0.31 (~10pct of the variance explained).
This section is entirely deleted in the new version - but we do agree that this sentence was incorrect.
-Typo at L610: "wider constrained range wider"
Thanks, fixed.
-L654: In terms of multi-metric approches, the authors may wish to cite the "cloud-controlling factor" approach (see Klein et al for a recent review) which has recently shown promise for constraining cloud feedbacks.
Thanks for this. Completely agreed that there is an argument for greater robustness through the consideration of "bottom-up" decomposition of net feedbacks, such as that demonstrated in the Klein paper. We've added a paragraph on this topic in the discussion.
References:
Williamson, D. B., & Sansom, P. G. (2019). How are emergent constraints quantifying uncertainty and what do they leave behind?. Bulletin of the American Meteorological Society, 100(12), 2571-2588.
Klein S.A., Hall A., Norris J.R., Pincus R. (2017) Low-Cloud Feedbacks from Cloud-Controlling Factors: A Review. In: Pincus R., Winker D., Bony S., Stevens B. (eds) Shallow Clouds, Water Vapor, Circulation, and Climate Sensitivity. Space Sciences Series of ISSI, vol 65. Springer, Cham.
Hawkins, E., & Sutton, R. (2009). The potential to narrow uncertainty in regional climate predictions. Bulletin of the American Meteorological Society, 90(8), 1095-1108.Deser, C., Phillips, A., Bourdette, V., & Teng, H. (2012). Uncertainty in climate change projections: the role of internal variability. Climate dynamics, 38(3), 527-546.
Hawkins, E., Smith, R. S., Gregory, J. M., & Stainforth, D. A. (2016). Irreducible uncertainty in near-term climate projections. Climate Dynamics, 46(11), 3807-3819.
Sriver, R. L., Forest, C. E., & Keller, K. (2015). Effects of initial conditions uncertainty on regional climate variability: An analysis using a low‐resolution CESM ensemble. Geophysical Research Letters, 42(13), 5468-5476.
Armour KC (2017) Energy budget constraints on climate sensitivity in light of inconstant climate feedbacks, Nature Climate Change, 7, 331-335
Bretherton, C. and Caldwell, P.: Combining Emergent Constraints for Climate Sensitivity, Journal of Climate, 33(17), 7413–7430. 2020
Caldwell, P. M., Bretherton, C. S., Zelinka, M. D., Klein, S. A., Santer, B. D. and Sanderson, B. M.: Statistical significance of climate sensitivity predictors obtained by data mining, Geophysical Research Letters, 41(5), 1803–1808, doi:10.1002/2014gl059205, 2014.
Caldwell, P. M., Zelinka, M. D. and Klein, S. A.: Evaluating Emergent Constraints on Equilibrium Climate Sensitivity, Journal of Climate, 31(10), 3921–3942. 2018
Geoffroy, O., Saint-Martin, D., Olivié, D. J. L., Voldoire, A., Bellon, G. and Tytéca, S.: Transient Climate Response in a Two-Layer Energy-Balance Model. Part I: Analytical Solution and Parameter Calibration Using CMIP5 AOGCM Experiments, J. Clim., 26(6), 1841–1857, 2013a.
Geoffroy, O., Saint-Martin, D., Bellon, G., Voldoire, A., Olivié, D. J. L. and Tytéca, S.: Transient Climate Response in a Two-Layer Energy-Balance Model. Part II: Representation of the Efficacy of Deep-Ocean Heat Uptake and Validation for CMIP5 AOGCMs, Journal of Climate, 26(6), 1859–1876. 2013b.
Lutsko, N. J., & Popp, M. (2019). Probing the sources of uncertainty in transient warming on different timescales. Geophysical Research Letters, 46, 11367– 11377
Schlund, M., Lauer, A., Gentine, P., Sherwood S. C. and Eyring, V. (2020) Emergent constraints on equilibrium climate sensitivity in CMIP5: do they hold for CMIP6? Earth Syst. Dynam., 11, 1233–1258.
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AC2: 'Reply on RC2', Ben Sanderson, 30 Apr 2021
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RC3: 'Comment on esd-2020-85', Anonymous Referee #3, 17 Mar 2021
Summary:
The authors highlight the disagreement present between different estimates of the same quantity arising from multiple single metric emergent constraints and the confusion this may cause. They claim that the cause of this disagreement is over-simplified process representation and a lack of diversity among climate models, and illustrate their argument using a class of simple climate models.
Overall I find little to criticise, except that the manuscript reads more like a review than an original research paper. The discussion of the different classes of emergent constraints largely reflects what has been written elsewhere (and cited within the manuscript. The main original contribution appears to be the illustrative example, which is informative and welcome. The generality of the conclusions from such an extreme example is perhaps questionable, but many processes within climate models are parametrised equally simply, or more so.
Minor points:
Lines 17-18: From a purely statistical perspective there is no contradiction here. Inferences about the same quantity derived from different lines of evidence are not expected to be the same. As argued by Williamson and Sansom (2019), it is likely that many of these estimates are over-confident. But even if a more appropriate uncertainty quantification were carried out, the inferences would not and should not be the same. However, I accept that this is confusing for policy makers.
Line 19: More likely than what? This is a leading statement, the authors only show that this is one possible explanation for emergent behaviour.
Lines 66-67: A constraint disappearing in later generations of climate models is not necessarily proof that the constraint was spurious. Convergence among models may make the spread among the observable and/or the target quantity to small for a “significant” relationship to be detectable, the relationship may even appear to change sign. Although, convergence has its own caveats if it is not due to advances in knowledge but rather common acceptance of a least bad solution.
Lines 93-95: The pseudo-Bayesian approaches cited have very limited applicability, and most principled statistical approaches to the analysis of emergent constraints rely on regression analysis which does not imply model weights.
Line 98: Some level of subjectivity is unavoidable, the idea of objectivity in science where data are interpreted through any model is a delusion. The resampling approach used in the following paragraph applies avoids making parametric assumptions about probability distributions but implies certain assumptions of its own which aren’t clearly stated.
Lines 138-141: The correlation between the Cox and Sherwood D constraints is relatively week and unlikely to be statistically “significant”.
Lines 215-218: See my previous comment on Lines 66-67.
Line 369: What is meant by a meaningful constraint? The two later model indicates a reduction in uncertainty.
Line 369: Figure 2d?
Line 654: Karpechko et al. 2013 (DOI: 10.1175/JAS-D-13-071.1) should be cited here.
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AC3: 'Reply on RC3', Ben Sanderson, 30 Apr 2021
The authors highlight the disagreement present between different estimates of the same quantity arising from multiple single metric emergent constraints and the confusion this may cause. They claim that the cause of this disagreement is over-simplified process representation and a lack of diversity among climate models, and illustrate their argument using a class of simple climate models.
Agreed. Many thanks to the reviewer for the comments and careful review.
Overall I find little to criticise, except that the manuscript reads more like a review than an original research paper.}
This opinion was reflected in all the reviews (and the authors broadly agree). Given this, we requested that the journal reclassify the paper and we new present the study as a review.
The discussion of the different classes of emergent constraints largely reflects what has been written elsewhere (and cited within the manuscript. The main original contribution appears to be the illustrative example, which is informative and welcome. The generality of the conclusions from such an extreme example is perhaps questionable, but many processes within climate models are parametrised equally simply, or more so.
Thanks for the comments. We agree that the simple model is an extreme example of a structural error, which cannot be generalised to parametric limitations in CMIP-class models. However, we do think that the simple example serves to illustrate the potential for how structural errors could project onto emergent constraints, and ultimately to encourage future studies to consider how ensemble-derived relationships could, in fact, arise from simple common parametric assumptions which exist throughout the ensemble. We have endeavored in the revisions to sharpen our language in making the distinction between the toy model and the discussion of CMIP structural errors.
Minor points:
Lines 17-18: From a purely statistical perspective there is no contradiction here. Inferences about the same quantity derived from different lines of evidence are not expected to be the same. As argued by Williamson and Sansom (2019), it is likely that many of these estimates are over-confident. But even if a more appropriate uncertainty quantification were carried out, the inferences would not and should not be the same. However, I accept that this is confusing for policy makers.
Agreed, apologies for the lazy wording - we've revised as:
"The prevalence of this thinking has led to literature which made confident, yet inconsistent between studies, claims on the probability bounds of key climate variables. "
In general, we agree that there is the potential to use multiple ECs and combine lines of independent evidence. However, we would argue that the majority of EC studies do not present their results as likelihoods which could inform a combined posterior or body of evidence - rather they present their headline result as an absolute probability (see, e.g. Cox 2018, Nijsse 2020, Jiménez-de-la-Cuesta 2019).
Line 19: More likely than what? This is a leading statement, the authors only show that this is one possible explanation for emergent behaviourAgreed. We've revised the sentence as follows:
"Here, we illustrate that strong ensemble relationships between observables and future climate can arise from common structural assumptions with few degrees of freedom. Such cases have the potential to produce strong, yet overconfident constraints when processes are represented in a common, oversimplified fashion throughout the ensemble, where we might have low confidence in the behaviour of the process in a future climate. "
Lines 66-67: A constraint disappearing in later generations of climate models is not necessarily proof that the constraint was spurious. Convergence among models may make the spread among the observable and/or the target quantity to small for a “significant” relationship to be detectable, the relationship may even appear to change sign. Although, convergence has its own caveats if it is not due to advances in knowledge but rather common acceptance of a least bad solution.
We agree - the original sentence was sloppily worded. We intended to convey the case (as in Klein and Hall 2015), where the new models are outliers in the original constraint, thus degrading confidence in the relationship when the two ensembles are combined. We've revised the sentence to clarify.
Lines 93-95: The pseudo-Bayesian approaches cited have very limited applicability, and most principled statistical approaches to the analysis of emergent constraints rely on regression analysis which does not imply model weights.
Agreed, thanks. Added the caveat that these studies do not test the underlying implicit assumptions of the regression framework.
Line 98: Some level of subjectivity is unavoidable, the idea of objectivity in science where data are interpreted through any model is a delusion. The resampling approach used in the following paragraph applies avoids making parametric assumptions about probability distributions but implies certain assumptions of its own which aren’t clearly stated.
Agreed. The analysis has been removed in the revision, following comments from other reviewers, but we fully agree on the impossibility of truly objective analysis
Lines 138-141: The correlation between the Cox and Sherwood D constraints is relatively week and unlikely to be statistically “significant”.Agreed - apologies for the error. The relevant section has been deleted.
Lines 215-218: See my previous comment on Lines 66-67.}
Again, the wording was sloppy. Now:
"If an emergent constraint has been found in an MME (providing it has not been demonstrated to be statistically spurious by, for example, additional models which significantly weaken the correlation (Klein and Hall 2015))..."
Line 369: What is meant by a meaningful constraint? The two later model indicates a reduction in uncertainty.
Sorry, reference error. The sentence (now reworded) refers to Figure 1d - which shows that T70 is not strongly correlated with T280 in the 2 layer model ensemble.
Line 369: Figure 2d?
Yes, indeed - see above.Line 654: Karpechko et al. 2013 (DOI: 10.1175/JAS-D-13-071.1) should be cited here.
Agreed - added.
References
Cox, P. M., Huntingford, C., & Williamson, M. S. (2018). Emergent constraint on equilibrium climate sensitivity from global temperature variability. Nature, 553(7688), 319-322.
Nijsse, F. J. M. M., Cox, P. M., & Williamson, M. S. (2020). An emergent constraint on Transient Climate Response from simulated historical warming in CMIP6 models. Earth System Dynamics Discussions, 2020, 1-14.
Jiménez-de-la-Cuesta, D., & Mauritsen, T. (2019). Emergent constraints on Earth’s transient and equilibrium response to doubled CO 2 from post-1970s global warming. Nature Geoscience, 12(11), 902-905.
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AC3: 'Reply on RC3', Ben Sanderson, 30 Apr 2021
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CC1: 'Comment on esd-2020-85', Richard Rosen, 19 Mar 2021
While the three comments from reviewers so far seem to complain that the article in question is more like a review article than an article describing new research, I think this is a good reason to publish it, not a negative. While I am not a researcher who develops earth system models, in most areas of applied science there are far too many "original" research articles, and far too few articles discussing the strengths and weaknesses of how very complex models like ESMs are being developed and applied in making forecasts. After CWIP6 it is certainly time for climate system modelers to step back and assess the value of trying to analyze multi-model ensembles, especially when the results of so many models are so different. Needless to say, policy makers probably do not have the slightest idea of how to evaluate these differences.
The gist of the current article under review is that the key focus in developing climate science models, like all scientifically-based models, must be on the scientific basis for each major process modeled. Thus, rather than try to use emerging constraits to help make forecasts more accurate, one should focus on improving the scientific basis for how each process is modeled. To me, this implies trying to get more scientific concensus as to how each process should be modeled, and not to think that diverse methodologies are helpful. This is especially true when the number of degrees of freedom is too limited in order to get reasonably accurate backcasts for each process in all past time periods. This issue exists for other types of scientific models, and even applies to more policy oriented models like the integrated assessment models used to create climate change mitigation scenarios.
My takeaway from the article is that having fewer earth systems models that include more concensual methodologies for each process modeled would be better than the current situation. More cooperation between climate scientists, then, would be helpful for make each process modeled in a sufficiently detailed and more scientifically accurate way, rather than the more approximate approaches that different modeling groups currently take. To summarize, I think the implication of this article, whether or not the authors would want to say this, is that there are too many different modeling groups in the world, and thus too many different models, each of which is too simplistic, and which don't agree with each other sufficiently to have much comfort in the overall progress of the field. Unfortunately, there is a tendency in most fields for too many research groups to exist, often supported by their national governments, which tends to prevent greater scientific cooperation and agreement between model experts because they focus their work on their own models. Competition is not always a plus whether in dealing with science or other social issues. The right balance needs to be achieved between cooperation and competition to maximize scientific progress, and the field of earth system modeling is no exception.
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AC4: 'Reply on CC1', Ben Sanderson, 30 Apr 2021
While the three comments from reviewers so far seem to complain that the article in question is more like a review article than an article describing new research, I think this is a good reason to publish it, not a negative. While I am not a researcher who develops earth system models, in most areas of applied science there are far too many "original" research articles, and far too few articles discussing the strengths and weaknesses of how very complex models like ESMs are being developed and applied in making forecasts. After CWIP6 it is certainly time for climate system modelers to step back and assess the value of trying to analyze multi-model ensembles, especially when the results of so many models are so different. Needless to say, policy makers probably do not have the slightest idea of how to evaluate these differences.
Many thanks to the commenter for their response to our study. We agree that often in literature which assesses high level ensemble relationships and distributions, there is a lack of consideration of the fundamental assumptions which might be common between models in the ensemble, and the degree to which these assumptions might influence our confidence in projections. It was certainly our aim in this study to highlight - for the particular application of emergent constraint literature, how such consideration could result in overconfidence in some studies published to date.
The gist of the current article under review is that the key focus in developing climate science models, like all scientifically-based models, must be on the scientific basis for each major process modeled. Thus, rather than try to use emergent constraits to help make forecasts more accurate, one should focus on improving the scientific basis for how each process is modeled.
Agreed
To me, this implies trying to get more scientific concensus as to how each process should be modeled, and not to think that diverse methodologies are helpful.
We would disagree on this point. Diverse methodolgies to represent a process are invaluable to represent uncertainty in a process and how it might evolve under future climate conditions. In some ways, the greatest danger is the perception of diversity in methodology when in fact there are a number of processes in ESMs where there are common or similar parameterisation schemes across the ensemble, effectively differing only in parameter values (e.g. soil respiration-temperature relationships). The ensemble can thus produce very strong internal relationships (because both future and past changes are a function of the same small set of parameters), but the constrained result excludes uncertainty associated with aspects of the process which are not represented in the current set of models.
This is especially true when the number of degrees of freedom is too limited in order to get reasonably accurate backcasts for each process in all past time periods. This issue exists for other types of scientific models, and even applies to more policy oriented models like the integrated assessment models used to create climate change mitigation scenarios.
Agreed (especially for IAMs). For Earth System Models, hindcasts are standard, but we agree that there is the strong capacity for compensating errors in reproducing historical climate change (in forcing, feedback and heat uptake - for example, in the case of transient global mean temperature changes), such that the data is insufficient to constrain some of the key degrees of freedom which control the dynamics of the system under mitigation. There is also - as you suggest, a tendancy to focus on aspects of historical performance which the models can reproduce - while ignoring aspects which the models cannot reproduce. A recent talk by Cristian Proistosescu on a paper in preparation discussed an excellent example of this in the failure of current generation models to represent recent tropical warming patterns, which have the capacity to bias estimates of global climate senstivity constrained by recent warming ( https://www.youtube.com/watch?v=5cO1TQtGyHc&t=17s )
My takeaway from the article is that having fewer earth systems models that include more concensual methodologies for each process modeled would be better than the current situation. More cooperation between climate scientists, then, would be helpful for make each process modeled in a sufficiently detailed and more scientifically accurate way, rather than the more approximate approaches that different modeling groups currently take.
There is an important discussion to be had on how to approach the modeling problem going forward to best represent uncertainty in projections. We would argue that a diversity of approaches is useful, perhaps essential, but the current ad-hoc sampling of structural assumptions, lack of consistent parameter sampling and treatment of the mutli-model archive as a distribution of equally plausible models represents a genuine problem. Weighting strategies might address some of these issues (see Brunner 2020, Sanderson 2017), as could operational parameter perturbation experiments in climate modeling (see Rostron 2020). But, as the commenter suggests, there is potential to think beyond what is possible in the current multi-center approach, and Fisher and Koven (2020) laid out a perspective for land surface modeling which considered the representation of structural process uncertainty within a common framework.
To summarize, I think the implication of this article, whether or not the authors would want to say this, is that there are too many different modeling groups in the world, and thus too many different models, each of which is too simplistic, and which don't agree with each other sufficiently to have much comfort in the overall progress of the field.
We don't see a problem with diversity of approaches per se, but we do agree that not enough focus is given to the structural assumptions within models - and this problem is particularly acute in the application of emergent constraints to an ensemble of models which in many cases share assumptions. From a climate risk perspective, our position is that greater focus could be placed on what current models might be missing, rather than on further constraining a distribution of projections of future change which is already a collection of best-estimates and ill-suited to the assessment of tail risks for future impacts.
Unfortunately, there is a tendency in most fields for too many research groups to exist, often supported by their national governments, which tends to prevent greater scientific cooperation and agreement between model experts because they focus their work on their own models. Competition is not always a plus whether in dealing with science or other social issues. The right balance needs to be achieved between cooperation and competition to maximize scientific progress, and the field of earth system modeling is no exception.
We broadly agree - that there are huge benefits to open, collaborative science which are often impeded by national interests and funding strategies. We would note also that there are some fine existing examples of collaborative science in climate modeling in the field, which successfully span borders - aided substantially by the progress of github and community development tools over the last decade (see the Community Earth System Model https://github.com/ESCOMP/CESM , the FATES land surface model https://github.com/NGEET/fates-release , and the FAIR simple climate model https://github.com/OMS-NetZero/FAIR ).
Brunner, L., Pendergrass, A. G., Lehner, F., Merrifield, A. L., Lorenz, R., & Knutti, R. (2020). Reduced global warming from CMIP6 projections when weighting models by performance and independence. Earth System Dynamics, 11(4), 995-1012.
Sanderson, B. M., Wehner, M., & Knutti, R. (2017). Skill and independence weighting for multi-model assessments. Geoscientific Model Development, 10(6), 2379-2395.
Rostron, J. W., Sexton, D. M., McSweeney, C. F., Yamazaki, K., Andrews, T., Furtado, K., ... & Tsushima, Y. (2020). The impact of performance filtering on climate feedbacks in a perturbed parameter ensemble. Climate Dynamics, 55, 521-551.
Fisher, R. A., & Koven, C. D. (2020). Perspectives on the future of land surface models and the challenges of representing complex terrestrial systems. Journal of Advances in Modeling Earth Systems, 12(4), e2018MS001453.
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AC4: 'Reply on CC1', Ben Sanderson, 30 Apr 2021
Benjamin M. Sanderson et al.
Benjamin M. Sanderson et al.
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