The Future of Climate Modelling: Weather Details, Macroweather Stochastics—Or Both?
Round 1
Reviewer 1 Report
Report on "The Future of Climate Modelling: Should We Chase Deterministic Details or Use Stochastic Models?" by Shaun Lovejoy
I'm sorry that this report has to be rather long, because it tries to deal with very many tricky issues. In brief, I cannot recommend publication of the present paper, but strongly recommend a rewrite as detailed at the far end of this report.
The title and much of the text prompt me to ask, why this exclusive either-or? Why not do both, deterministic and stochastic?
After all, to take a simpler example, it's well accepted that our best understanding of gas dynamics draws on both kinds of approach. It's useful to "chase details" of the molecular dynamics and individual molecular collisions, even down to the quantum level -- taking a short-timescale view -- alongside paying attention to the emergent long-timescale statistics such as temperature, pressure, and the Maxwell distribution. Above all it's useful, I'd argue, to see how the two kinds of approach complement and inform each other and help to achieve an in-depth overall understanding, recognizing that all the different levels of modeling have their uses, their strengths, and their weaknesses.
To be sure, in the case of gases the long-timescale statistics turn out to be insensitive to many of the collision details. However, at the very least it's useful for this to be shown, and well understood, rather than just asserted. Indeed the author's own figure 1 can be read as making the same point, that all the "different levels of modeling and understanding" (line 245) are useful, especially when their interrelation is well understood. One might add that there are some important applications, such as spacecraft re-entry in which, practically speaking, one really does need to use more than one level of modeling.
There are five main reasons why I cannot recommend publication of the paper as it stands, despite figure 1.
The first is the exclusivity already mentioned. I cannot accept the paper's message -- strongly asserted again and again -- that detail-chasing climate models are useless. The details they chase are far less simple than molecular collisions in gases; and it is far less simple to determine how the details affect longer-timescale statistics including, many would argue, the statistics of extreme weather events -- the all-important tails of the relevant PDFs -- as exemplified by the recent devastation of Durban and its environs by rainstorms in South Africa.
I'd be willing to take seriously a more nuanced advocacy, saying that stochastic models of the kind the author studies are interesting and useful alongside various other kinds of model -- giving alternative views of what, after all, is a formidably complicated problem, the problem of climate change and weather extremes over timescales ranging from minutes to tens of millions of years.
It would be wonderful if, for instance, the theories around multifractal objects could be shown to be useful. In lines 264-6 we read that "multifractal cascades... account for the atmosphere's enormous intermittency including the fact that most of its energy and other fluxes are concentrated in violent, extremely sparse (fractal) regions". Perhaps this is indeed connected with the devastation from extreme weather events in the real world. However, it seems to me that improvements in detail-chasing models would have to be part of any such story. Many of the weather extremes and their consequences, such as flash flooding and mudslides, depend on small-scale, short-lived details.
The second reason why I cannot recommend publication is that, in my judgement, it is profoundly misleading to give the impression, even inadvertently, that a single multifractal or scaling paradigm -- originating in studies of fluid-dynamical turbulence -- must apply to everything else in the real world (e.g., everything mentioned in connection with figure 3, including the glacial-interglacial cycles, which have been shown by meticulous paleoclimatic studies to depend on many other things including slow carbonate chemistry of the ocean and its sediments, and delayed isostatic lithosphere-asthenosphere rebound during deglaciations. Such rebound is probably crucial for instance to the spectral peak near Delta t ~ 10^5 years in figure 3; see for instance Abe-Ouchi et al., Nature 500, 190-193, 2013).
The third reason is just that the standard of writing is abysmal. The paper is put forward as a review. Therefore, surely, it should try to be intelligible and informative to a non-specialist. On the contrary, however, it's big on hype but almost negligible on informativeness. The reader encounters a welter of impressive sounding specialist terms, mostly undefined, and is in effect being told to learn what they mean by reading the 40 or so cited papers by the author and his co-workers.
The use of language is often sloppy and confusing, for example conflating Bayesian likelihoods with probabilities (line 499), which in standard Bayesian terminology are two different things, and conflating symmetries with conservation relations, also two different things even if often related. (See on line 421 "other symmetries, the obvious one being energy conservation.") In line 355 we suddenly encounter an undefined technical term "upper benthic", whose meaning is impossible to guess from the usual ocean-bottom connotation of "benthic". There are countless other sloppinesses and undefined specialist terms. I can guess that "scaling symmetries" (lines 233, 416-8) must have something to do with self-similarity, fractals, and power-law decay, but there isn't even a hint of an explanation, nor even a clear statement, let alone any hint about what the corresponding conservation relations might be.
On line 432 we are told that an important character in the drama, eq (3) for the global-average temperature T(t), depends on "using the correct conductive-radiative surface boundary conditions... to avoid a key approximation". Again there's no hint as to what these vague words could possibly mean. Here the lack of information is not even supported by a citation. On line 439 a hint is dropped that "the correct... boundary conditions" involve some kind of power law. Still no information as to what variable is raised to what power, let alone why such a power law should be "the correct" law. Many readers would surely be skeptical about such a claim. In the real system we have a multilayered ocean with different timescales for changes over different depths. Simple exponential behavior, Newton's law of cooling, may well be wrong, but simple power-law behavior may well be wrong too.
And as soon as eq (3) is introduced, in striking and interesting contrast to eq (1) -- this was the first point in the paper where my own interest was sparked -- couldn't it be presented in a more focused way? Couldn't the reader at least be told straight away that eq (3) has (if I'm not miscalculating) a Green's function that decays like the square root of t, again in striking contrast to the familiar exponential decay of the Green's function for eq (1)? Admittedly, this point does emerge 26 lines later, on line 459, albeit misleadingly presented there as applying only to a sudden CO_2 doubling rather than, in a completely general way, to any impulsive forcing whatever.
It is claimed that the equations for T(t) respect "scale and energy symmetries" together, but then it is immediately suggested (line 425) that this applies not only to eqs (3) and (4) but also to the Budyko-Sellers model, eq (1). More confusion. Doesn't the author want to say that only eqs (3) and (4) respect scaling, due to their power-law Green's functions, while eq (1) with its exponential Green's function does not?
Adding to the confusion is an extraordinarily sloppy use of math notation. There are very many typos, far more than an occasional slip. For instance there's an all-important parameter set (h, tau, s, a, n). The Greek letter tau is often mistyped as t, even though t also denotes the time variable in T(t). Time and temperature changes Delta t and Delta T are often mistyped as Dt
and DT (e.g. line 360; contrast with figure 3). The dissipation parameter of standard turbulence theory, Kolmogorov's epsilon, is mistyped as e (lines 372-3, 384-5). Notice also the superscripts that aren't shown as superscripts.
I could go on and on. Some of the typos aren't too difficult to decipher, but their prevalence does little to build the reader's confidence in an author who'd like to persuade us that he is an authority on the precise and beautiful math of stochastic modeling. I for one, being potentially interested but not especially expert, would have appreciated learning something about the math from an informative, clear, and consistent detailed exposition by such an authority.
The fourth reason why I cannot recommend publication is that the results actually presented fall far short of what seems to have been promised. After the first ten or so pages, replete with hype about turbulence theory, Richardson cascades, scaling theory, multifractals, and extreme fluctuations, the reader eventually learns on reading the rest of the paper that the work actually reported, see eq (4) and figures 4-7, is entirely focused on the time series T(t) of global-average surface temperatures. What is actually done is to fit a 5-parameter model for T(t), which is either eq (4) or another, unspecified equation called "SCRF" (lines 622-4), to climate data and/or to climate model output (from a CMIP multi-model ensemble). With 5 disposable parameters, it is no big deal that the single variable T(t) of such a model can be made to mimic the data, and/or the climate model outputs, more or less closely.
The author says that data analysis or climate-model output were used to influence the parameter values, but once again fails to make it clear just how that was done in each case, and how much flexibility was allowed. On a specific point, I am skeptical that the parameter tau, the single relaxation time in eq (4), should be as short as several years (line 516, noting again
that t is a typo for tau). This, and the very use of a single relaxation time, ignores for instance the range of longer timescales of the upper ocean and deep ocean, and in the CMIP climate models. Another undefined tehnical term "credible interval" or "CI" is used here. The text says "see below", and the term reappears in two subsequent locations, lines 537, 550, but the reader looks in vain for some kind of definition or clarification. We were told on line 530 that CI's are "parametric uncertainties", but that is hardly informative either.
The fifth reason why I cannot recommend publication is the author's argument, heavily emphasized, that one may judge a model's appropriateness solely by its internal uncertainty. The smaller the internal certainty the better the model, the author seems to keep saying (lines 22, 95, 113, 122, 149, 193). Yes, model uncertainties, or variances, are of interest, as are PDF tails and other internal model properties. However, internal model properties including uncertainties are not the same thing as real-world properties, and not the same thing as closeness to the real world.
Let me say finally that, if the author could bring himself to rewrite the paper in a more tightly focused and informative way, arriving at eq (4) and figures 4-6, and of course the SCRF equation and figure 7, as quickly as possible, then I'd be happy to recommend publication provided also that the author drops the unwarranted assertions that deterministic models are useless. That would surely win over many more readers.
Most of the remarks about other theoretical constructs, such as multifractals and scaling, could be postponed to a concluding section in which the perspective is broadened. They could be postponed except to the extent that they motivate the power-law Green's functions of eq (4) and (presumably) SCRF.
A perspective-broadening Conclusions would be a good place to briefly advertise, for instance, the promise of mulifractals in helping to understand weather extremes -- acknowledging that the question of extremes goes far beyond eq (4) and figures 4-7. This would give a more coherent and persuasive motivation than the endless hype in the current pages 1-10, most of which would be better discarded, especially since it gives the false impression, or at least the vague suggestion, that a single paradigm should be applicable to the entire range of timescales shown in figure 3.
In the body of the paper there would then be more space for specifying the all-important forcing functions F_ext and F_int used to generate figs 4-7 (at present completely unspecified) together with a more intelligible explanation of how they, and the parameter values (h, tau, s, a, n) were arrived at. Come to think of it, there's a sixth parameter, isn't there? Even if the white-noise forcing F_int is Gaussian, we still need to know its variance.
Author Response
Comments attached. Note in particular the question of commentary versus review and the unfortunate change in fonts.
Author Response File: 
Author Response.pdf
Reviewer 2 Report
General comments:
Macroweather. A very interesting idea! I enjoyed reading the manuscript and agree the scientific logic presented by this article. "Chasing details" might not be a correct approach for long-term climate trend prediction. People have to focus on factors that are "relevant" to a subject they study. Interestingly, a similar idea but in "opposite" treatment has been recently published in this journal about numerical weather prediction (NWP). Since they want to predict "disturbances" related to daily weather, the background "climate" part doesn't need to be predicted. Therefore, they propose to use "anomaly" format of the atmospheric governing equations to build an NWP model by eliminating climate prediction. Since that work and yours are in the same general thinking about the earth atmospheric problems, you might cite that work. Here is the mentioned reference:
Qian, W.; Du, J. Anomaly Format of Atmospheric Governing Equations with Climate as a Reference Atmosphere. Meteorology 2022, 1, 127-141. https://doi.org/10.3390/meteorology1020008
Below are a few more comments about your manuscript. A minor revision is needed before its publication.
(1) The reference format is not correct for this journal and needs to be corrected.
(2) Inside the text, the temperature unit "degree symbol" is not in the correct upper-right position, so are the powers of scientific expression such as 10-3.
(3) Some math terms within text such as DT(Dt)≈ DtH might look better if you use "insert equation" function to write them.
(4) Line 448: 0>h≥1. Is this correct?
(5) A possible reason for the increase of uncertainty in MME could be related to the improvement of models. Older models were poorer and neglected many complex physical processes, which leads to less sensitive to initial conditions (ICs). If this is true, the member spread of MME should decrease when model quality reaches to a level of "good enough" in a future moment if IC improves. Afterward, the forecast uncertain might saturate and remain at a similar constant level?
Author Response
Note that the paper was originally submitted as a commentary, then at the urging of the editor it was reclassified as a review. Finally, it would be more appropriate to reclassify it back as a commentary (see the reactions to referee1).
Also, I hope that the fonts were not changed (as they were last time), this eliminated Greek symbols and superscripts, subscripts.
See attachement for the full response.
Author Response File: Author Response.pdf
Round 2
Reviewer 1 Report
Please see attachment.
Comments for author File: Comments.pdf
Author Response
I assumed that the responses had to explain the changes. Therefore I combined the new draft with the responses into a single file.
Author Response File: Author Response.pdf
Round 3
Reviewer 1 Report
Please see the attachment.
Comments for author File: Comments.pdf
Author Response
I have attached a pdf that merges the responses with the revised text.
Please send a pdf version of the revised paper to the referee. This will prevent the line numbers from changing. Thanks.
Author Response File: Author Response.pdf
Round 4
Reviewer 1 Report
Please see the attachment.
Comments for author File: Comments.pdf
Author Response
The attached file is a revised manuscript with the responses to the referee merged at the end.
Author Response File: Author Response.pdf
