Improving the Scientific Foundation for Atmosphere-Land-Ocean Simulations: Report of a Workshop (2005)

Isaac M. Held

Geophysical Fluid Dynamics Laboratory-National Oceanic and Atmospheric Administration

Princeton, New Jersey

(DRAFT¹)

January 13, 2004

The problem of creating truly convincing numerical simulations of our Earth’s climate will remain a challenge for the next generation of climate scientists. Hopefully, the ever-increasing power of computers will make this task somewhat less frustrating than it is at present. But increasing computational power also raises issues as to how we would like to see climate modeling and the study of climate dynamics evolve in the 21st century. One of the key issues we will need to address is the widening gap between simulation and understanding. A change in emphasis in theoretical climate research is needed if we are to close this gap.

The complexity of the climate system presents a challenge to climate theory, and to the manner in which theory and observations interact, eliciting a range of responses. On the one hand, we try to simulate by capturing as much of

the dynamics as we can in comprehensive numerical models. On the other hand, we try to understand by simplifying and capturing the essence of a phenomenon in idealized models, or even with qualitative pictures. As our comprehensive models improve in quality, they more and more often become the primary tools by which theory confronts observations. The study of global warming is an especially good example of this trend. A handful of major modeling centers around the world compete in creating the most convincing climate simulations and the most reliable forecasts of climate change, while large observational efforts are mounted with the stated goal of improving these comprehensive models.

Due to the great practical value of simulations, and the opportunities provided by the continuing increases in computational power, the importance of understanding is occasionally questioned. What does it mean, after all, to understand a system as complex as the climate, when we cannot fully understand idealized nonlinear systems with only a few degrees of freedom?

Without attempting an all-encompassing definition, it is fair to say that we typically gain some understanding of a complex system by relating its behavior to that of other, especially simpler, systems. For sufficiently complex systems, we need a model hierarchy on which to base our understanding, describing how the dynamics change as key sources of complexity are added or subtracted. Our understanding benefits from appreciation of the interrelationships among all elements of the hierarchy.

The importance of such a hierarchy for climate modeling has often been emphasized. See Hoskins (1983) for a particularly eloquent discussion. But despite notable exceptions in a few subfields, climate theory has not, in my opinion, been very successful at hierarchy construction.

Consider by analogy another field that must deal with exceedingly complex systems—molecular biology. How is it that biologists have made such dramatic and steady progress in sorting out the human genome and the actions and interactions of the thousands of proteins of which we are constructed? Without doubt, one key has been that nature has provided us with a hierarchy of biological systems of increasing complexity amenable to experimental manipulation, ranging from bacteria to fruit fly to mouse to man. Furthermore, the nature of evolution assures us that much of what we learn from simpler organisms is directly relevant to deciphering the workings of their more complex relatives. What good fortune for the biological sciences to be presented with precisely the kind of hierarchy needed to understand a complex system! Imagine how much progress would have been made if one were limited to studying man alone.

Unfortunately, nature has not provided us with simpler climate systems that form such a beautiful hierarchy. Planetary atmospheres provide us with some insights into the range of behaviors possible, but they are few in number, and each planet has its own idiosyncrasies. While their study has connected to

terrestrial climate theory on occasion, the influence has not been systematic. Laboratory simulations of rotating and/or convecting fluids remain a valuable and underutilized resource, but they cannot address many of our most complex problems. We are left with the necessity of constructing our own hierarchies of climate models.

Because nature has provided the biological hierarchy, it is much easier to focus the attention of biologists on a few representatives of the key evolutionary steps towards greater complexity. And such a focus is central to success. If every molecular biologist had simply studied his or her own favorite bacterium or insect, rather than focusing so intensively on E. coli or Drosophila melanogaster, it is safe to assume that progress would have been far less rapid.

It is emblematic of our problem that studying the biological hierarchy is experimental science, while constructing and studying climate hierarchies is theoretical science. One can justify studying E. coli not only because it shares many fundamental genetic mechanisms with all cells, but also because it exists, after all, and it and its close bacterial relatives affect the world in ways that are worth understanding at the molecular level in their own right. Elements of a climate model hierarchy are generally only of interest to climate theorists.

A biologist need not convince her colleagues that the model system she is advocating for intensive study is well designed or well posed, but only that it fills an important niche in the hierarchy of complexity and that it is convenient for study. Climate theorists are faced with the difficult task of both constructing a hierarchy of models and somehow focusing the attention of the community on a few of these models so that our efforts accumulate efficiently. Even if one believes that one has defined the E. coli of climate models, it is difficult to energize (and fund) a significant number of researchers to take this model seriously and devote substantial parts of their careers to its study.

And yet, despite the extra burden of trying to create a consensus as to what the appropriate climate model hierarchies are, the construction of such hierarchies must, I believe, be a central goal of climate theory in the 21st century. There are no alternatives if we want to understand the climate system and our comprehensive climate models. Our understanding will be embedded within these hierarchies.

Why should we care that we do not understand our comprehensive climate models as dynamical systems in their own right? Does this matter if our primary goal happens to be to improve our simulations, rather than to create a subjective feeling of satisfaction in the mind of some climate theorist?

Suppose that one can divide a climate model into many small distinct components and that one can devise a testing and development strategy for each

of these modules in isolation (including the form of the interactions among these modules). If the components have been adequately tested, is there any need for an understanding of what happens when they are coupled? To the extent that one can break down the testing process into manageable pieces, this bottom-up, reductive strategy is without doubt an appropriate and efficient approach to model development. Understanding is needed at the level of the module in question, so as to ensure its fidelity to nature, but is there understanding to be gained as a higher, more holistic level, that is of value to the climate modeling enterprise? Are we better off limiting ourselves to trying to understand particular physical processes of climatic relevance?

The radiation code in atmospheric models (the clear-sky component, at least) is a good example. The broadband computations used in climate models are systematically tested against line-by-line computations based on the latest laboratory studies and field programs. When atmospheric observations and/or laboratory absorption studies require a modification to the underlying database (for example, with regard to water vapor continuum absorption), this new information makes its way more or less efficiently into the broadband climate model codes. Given this relatively convincing methodology, the (clear-sky) radiative flux component of climate models is generally treated with respect, evolving only when driven to do so by evidence of the sort outlined above.

Work towards devising similar methodologies for other model components is obviously of vital importance. But we are very far today from being able to construct our comprehensive climate models in this systematic fashion. Despite several major observational campaigns designed to guide us towards appropriate closures for deep moist convection, as an important example, there is little sense of convergence among existing atmospheric models. A program in which cloud-resolving simulations are systematically used as a middle ground between closure schemes and observations promises to improve this situation in the future, but there is still a long way to go.

When a fully satisfactory systematic bottom-up approach to model building is unavailable, the development process can be described, without any pejorative connotations intended whatsoever, as engineering, or even tinkering. (Our most famous inventors are often described as tinkerers!) Various ideas are put forward by the team building the model, based on their wisdom and experience, as well as their idiosyncratic interests and prejudices. To the extent that a modification to the model based on these ideas helps ameliorate a significant model deficiency, even if it is, serendipitously, a different deficiency than the one providing the original motivation, it is accepted into the model. Generated by these informed random walks, and being evaluated with different criteria of merit, the comprehensive climate models developed by various groups around the world evolve along distinct paths.

The value of a holistic understanding of climate dynamics for model development is in making this process more informed and less random, and thereby

more efficient. To the extent that we have little understanding of which aspects of a moist convection scheme are most important for exaggerating the double ITCZ in the East Pacific, or which help control the period of ENSO, then our search for ways to ameliorate our double ITCZ or improve our ENSO spectrum will be that much more random and less informed.

A holistic understanding of climate dynamics also helps in relating one comprehensive model to another. If stratosphere-troposphere interactions in one comprehensive model result in a trend in the North Atlantic Oscillation as a result of increasing carbon dioxide, but not in other models, how does one judge which is correct? Perhaps by confronting the models with observations—but precisely how does one do this? All models are imperfect, but which imperfections are most relevant to this problem? Inevitably, one needs to understand the differences between the models at some level. One can try to systematically and laboriously morph one model into the other, and heroic attempts of this kind have been attempted in various contexts and can be informative. Alternatively, one can construct more idealized models designed to capture the essence of the interaction in simpler systems, within which the climate dynamics community can focus more directly on the central issues. These idealized studies can then suggest optimal ways of categorizing or analyzing more comprehensive models.

Accepting that the kind of understanding that emerges from the construction and analysis of climate model hierarchies is important, and given the many efforts under way that are devoted to models of various levels of complexity, are there things we could do to make this effort more productive? I highlight two related tendencies that have slowed the systematic development of climate model hierarchies. (My own work illustrates these two tendencies nicely, and this discussion is as much a self-critique as it is one of the field more generally.)

There is a tendency in our field for a theoretically inclined researcher to design and build a model—on the basis of which he or she tries to create the case for some picture of a phenomenon or for the utility of some concept or approach—and then drop the model. The model is not intended, in many cases, to have a life of its own, but is rather a temporary expedient. In the limiting case, the model is not fully described and the result not fully reproducible. This tendency exists in those working with models at all levels of complexity. The focus is on the concept being put forward, not the model itself.

I do not mean to minimize the importance of the search for new concepts of general utility—this will always be one of the primary goals of all theoretical work. But we cannot limit ourselves to this conceptual approach. The claim is that the complexity of the climate system is such that we cannot make systematic progress towards understanding climate dynamics other than through model hierarchies. The design and refinement of these hierarchies require the accumulated wisdom of an assortment of scientists with different skills and incentives, and must in themselves be a central goal of our research.

Our goal must be to reduce the number of models that we analyze. Otherwise we are left with a string of interesting results, few of which have been intensively examined by more than two or three people, and which we never quite manage to relate to each other. (The body of theoretical work on the Madden-Julian Oscillation provides a good example of this problem, in my opinion.) But how can this inefficient deployment of our theoretical resources be avoided? The key, I feel, is elegance.

An elegant model is as elaborate as it needs to be to capture the essence of a particular source of complexity, but no more elaborate. Many of our models are more elaborate than they need be, and this is, I believe, the prime reason why it is difficult for the field as a whole to focus efficiently on a small number of models. If a particular scheme seems unnecessarily baroque, why should I use it as a basis for my own research? What lasting value will my study have? Why not change the model to better suit by specific interests?

Over-elaboration results in part from the pressure we all feel for our work to be relevant to the big issues in climate dynamics. This relevance generally requires a certain level of realism in one’s simulations, and this pressure to reach the required level of realism often pushes models towards ever-increasing elaboration. Yet, in the process one’s model often loses much of its attraction to other researchers.

We justify our research, to ourselves and others, by appealing to some mixture of short-term practical consequences and lasting value. High-end simulations are primarily driven by the need to meet practical applications, requiring them to be as realistic as possible given existing resources. These simulations need be of no lasting value, as they will be supplanted by ever more comprehensive models as computer resources increase. When global nonhydrostatic atmospheric models resolving deep moist convection become common in future decades, the global warming simulations obtained with the current generation of models will be of historical interest only. But the importance of the problem is such that we cannot wait for this to occur; we need to do our best now, knowing full well that these efforts will be obsolete within most of our lifetimes. While

there is no value in elaborating these comprehensive simulations in ways that have no practical consequences or no hope of confronting data, an emphasis on elegance can be counterproductive, as a large number of details may very well be needed to get things right quantitatively.

As we back off from this high end, the balance between elegance and realism becomes more of an issue. My reading of the literature is that elegance is often sacrificed unnecessarily, partly for the sake of a competition with comprehensive models. The latter seem, after all, to be extraordinarily inefficient at attacking many key climate problems. Yet, in an era of exponentially increasing computational power, this competition is often less valuable than we might like to admit, given the time scale at which studies become feasible at a more comprehensive level.

Elegance and lasting value are correlated. An elegant hierarchy of models upon which the field as a whole bases its understanding of the climate system can be of benefit to future generations for whom our comprehensive simulations will have become obsolete.

The health of climate theory/modeling in the coming decades is threatened by a growing gap between high-end simulations and idealized theoretical work. In order to fill this gap it is evident that research with a hierarchy of models is needed. But to be successful, this work must make progress towards two goals simultaneously. It must, on the one hand, make contact with the high-end simulations and improve the comprehensive model development process; otherwise it is irrelevant to that process, and, therefore, to all of the important applications built on our ability to simulate. On the other hand, it must proceed more systematically towards the creation of a hierarchy of lasting value, providing a solid framework within which our understanding of the climate system, and that of future generations, is embedded. Funding for climate dynamics should reflect this need to balance conceptual research, simulation, and hierarchy development.

Hoskins, B. J. 1983. Dynamical processes in the atmosphere and the use of models. Quart. J. Roy. Meteorol. Soc. 109:1-21.