# Lightning in a Bottle/Chapter 6

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Chapter Six

Why Bottle Lightning?

6.0 A Different Kind of Model

We’ve now explored several significant challenges that climatologists must consider when attempting to create models of the global climate that even approach verisimilitude. The global climate is chaotic in the sense that very small perturbations of its state at one time lead to exponentially diverging sequences of states at later times. The global climate is also non-linear in the sense that equations describing its behavior fail both the additivity and degree-1 homogeneity conditions. They fail these conditions primarily in virtue of the presence of a number of distinct feedbacks between the subsystems of the global climate.

In Chapter Four, we noted that while energy balance models in general are useful in virtue of their simplicity and ease of use, they fail to capture many of the nuances responsible for the behavior of the Earth’s climate: while things like radiative balance are (generally speaking) the dominant features driving climate evolution, attending only to the most powerful influences will not always yield a model capable of precise predictive success. We saw how the more specialized EMIC-family of models can help ameliorate the shortcomings of the simplest models, and while the breadth and power of EMICs is impressive, there is surely a niche left to be filled in our modeling ecosystem: the comprehensive, high-fidelity, as-close-to-complete-as-we-can-get class of climate models. Coupled global circulation models[1] (CGCMs) fill that niche, and strive for as much verisimilitude as possible given the technological constraints. In contrast to the rough-and-ready simplicity energy balance models and the individual specialization of EMICs, CGCMs are designed to be both general and detailed: they are designed to model as many of the important factors driving the Earth’s climate as well as they possibly can. This is a very tall order, and the project of crafting CGCMs raises serious problems that EBMs and EMICs both manage to avoid. Because of their comprehensiveness, though, they offer the best chance for a good all-things-considered set of predictions about the future of Earth’s climate.

The implementation of CGCMs is best understood as a careful balancing act between the considerations raised in Chapter Five. CGCMs deliberately incorporate facts about the interplay between atmospheric, oceanic, and terrestrial features of the global climate system, and thus directly confront many of the feedback mechanisms that regulate the interactions between those coupled subsystems of the Earth’s climate. It should come as no surprise, then, that most CGCMs prominently feature systems of nonlinear equations, and that one of the primary challenges of working with CGCMs revolves around how to handle these non-linearities. While the use of supercomputers to simulate the behavior of the global climate is absolutely essential if we’re to do any useful work with CGCMs, fundamental features of digital computers give rise to a set of serious challenges for researchers seeking to simulate the behavior of the global climate. The significance of these challenges must be carefully weighed against the potentially tremendous power of well-implemented CGCMs. In the end, I shall argue that CGCMs are best understood not as purely predictive models, but rather as artifacts whose role is to help us make decisions about how to proceed in our study of (and interaction with) the global climate.

6.1 Lewis Richardson’s Fabulous Forecast Machine

The dream of representing the world inside a machine--of generating a robust, detailed, real-time forecast of climate states--reaches all the way back to the early days of meteorology. In 1922, the English mathematician Lewis Richardson proposed a thought experiment that he called “the forecast factory.” The idea is so wonderfully articulated (and so far-seeing) that it is worth quoting at length here:

Imagine a large hall like a theatre, except that the circles and galleries go right round through the space usually occupied by the stage. The walls of this chamber are painted to form a map of the globe. The ceiling represents the north polar regions, England is in the gallery, the tropics in the upper circle, Australia on the dress circle, and the Antarctic in the pit. A myriad computers[2] are at work upon the weather of the part of the map where each sits, but each computer attends only to one equation or one part of an equation. The work of each region is coordinated by an official of higher rank. Numerous little ‘night signs’ display the instantaneous values so that neighboring computers can read them. Each number is thus displayed in three adjacent zones so as to maintain communication to the North and South on the map. From the floor of the pit a tall pillar rises to half the height of the hall. It carries a large pulpit on its top. In this sits the man in charge of the whole theatre; he is surrounded by several assistants and messengers. One of his duties is to maintain a uniform speed of progress in all parts of the globe. In this respect he is like the conductor of an orchestra in which the instruments are slide-rules and calculating machines. But instead of waving a baton he turns a beam of rosy light upon any region that is running ahead of the rest, and a beam of blue light upon those who are behindhand.

Four senior clerks in the central pulpit are collecting the future weather as fast as it is being computed, and dispatching it by pneumatic carrier to a quiet room. There it will be coded and telephoned to the radio transmitting station. Messengers carry piles of used computing forms down to a storehouse in the cellar.

In a neighboring building there is a research department, where they invent improvements. But there is much experimenting on a small scale before any change is made in the complex routine of the computing theatre. In a basement an enthusiast is observing eddies in the liquid lining of a huge spinning bowl, but so far the arithmetic proves the better way.[3] In another building are all the usual financial, correspondence, and administrative offices. Outside are playing fields, houses, mountains, and lakes, for it was thought that those who compute the weather should breathe of it freely.

Fig. 6.1

Artist’s conception of Lewis Richardson’s forecast factory[4]

Richardson’s forecast factory (Fig. 6.1) was based on an innovation in theoretical meteorology and applied mathematics: the first step toward integrating meteorology with atmospheric physics, and thus the first step toward connecting meteorology and climatology into a coherent discipline united by underlying mathematical similarities. Prior to the first decade of the 20th century, meteorologists spent the majority of their time each day charting the weather in their region--recording things like temperature, pressure, wind speed, precipitation, humidity, and so on over a small geographical area. These charts were meticulously filed by day and time, and when the meteorologist wished to make a forecast, he would simply consult the most current chart and then search his archives for a historical chart that was qualitatively similar. He would then examine how the subsequent charts for the earlier time had evolved, and would forecast something similar for the circumstance at hand.

This qualitative approach began to fall out of favor around the advent of World War I. In the first years of the 20th century, a Norwegian physicist named Vilhelm Bjerknes developed the first set of what scientist today would call “primitive equations” describing the dynamics of the atmosphere. Bjerknes’ equations, adapted primarily from the then-novel study of fluid dynamics, tracked four atmospheric variables--temperature, pressure, density, and humidity (water content)--along with three spatial variables, so that the state of the atmosphere could be represented in a realistic three-dimensional way. Bjerknes, that is, defined the first rigorous state space for atmospheric physics[5].

However, the nonlinearity and general ugliness of Bjerknes’ equations made their application prohibitively difficult. The differential equations coupling the variables together were far too messy to admit of an analytic solution in any but the most simplified circumstances. Richardson’s forecast factory, while never actually employed at the scale he envisioned, did contain a key methodological innovation that made Bjerknes’ equations practically tractable again: the conversion of differential equations to difference equations. While Bjerknes’ atmospheric physics equations were differential--that is, described infinitesimal variations in quantities over infinitesimal time-steps--Richardson’s converted equations tracked the same quantities as they varied by finite amounts over finite time-steps. Translating differential equations into difference equations opens the door to the possibility of generating numerical approximation of answers to otherwise intractable calculus problems. In cases like Bjerknes’ where we have a set of differential equations for which it’s impossible to discern any closed-form analytic solutions, numerical approximation by way of difference equations can be a godsend: it allows us to transform calculus into repeated arithmetic. More importantly, it allows us to approximate the solution to such problems using a discrete state machine--a digital computer.

6.2.0 General Circulation Models

Contemporary computational climate modeling has evolved from the combined insights of Bjerknes and Richardson. Designers of high-level Coupled General Circulation Models (CGCMs) build on developments in atmospheric physics and fluid dynamics. In atmospheric circulation models, the primitive equations track six basic variables across three dimensions[6]: surface pressure, horizontal wind components (in the x and y directions), temperature, moisture, and geopotential height. Oceanic circulation models are considerably more varied than their atmospheric cousins, reflecting the fact that oceanic models’ incorporation into high-level climate models is a fairly recent innovation (at least compared to the incorporation of atmospheric models). Until fairly recently, even sophisticated GCMs treated the oceans as a set of layered “slabs,” similar to the way the atmosphere is treated in simple energy balance models (see Chapter Four). The simple “slab” view of the ocean treats it as a series of three-dimensional layers stacked on top of one another, each with a particular heat capacity, but with minimal (or even no) dynamics linking them. Conversely (but just as simply), what ocean modelers call the “swamp model” of the ocean treats it as an infinitely thin “skin” on the surface of the Earth, with currents and dynamics that contribute to the state of the atmosphere but with no heat capacity of its own. Early CGCMs thus incorporated ocean modeling only as a kind of adjunct to the more sophisticated atmospheric models: the primary focus was on impact that ocean surface temperatures and/or currents had on the circulation of air in the atmosphere.

Methodological innovations in the last 15 years--combined with theoretical realizations about the importance of the oceans (especially the deep oceans) in regulating both the temperature and the carbon content of the atmosphere (see Section 5.2.2)--have driven the creation of more sophisticated oceanic models fusing these perspectives. Contemporary general ocean circulation models are at least as sophisticated as general atmospheric circulation models--and often more sophisticated. The presence of very significant constant vertical circulation in the oceans (in the form of currents like the thermohaline discussed in 5.2.2) means that there is a strong circulation between the layers (though not as strong as the vertical circulation in the atmosphere). Moreover, the staggering diversity and quantity of marine life--as well as the impact that they have on the dynamics of both the ocean and atmosphere--adds a wrinkle to oceanic modeling that has no real analog in atmospheric modeling.

Just as in Richardson’s forecast factory, global circulation models (both in the atmosphere and the ocean) are implemented on a grid (usually one that’s constructed on top of the latitude/longitude framework). This grid is constructed in three dimensions, and is divided into cells in which the actual equations of motion are applied. The size of the cells is constrained by a few factors, most significantly the computational resources available and the desired length of the time-step when the model is running. The first condition is fairly intuitive: smaller grids require both more computation (because the computer is forced to simulate the dynamics at a larger number of points) and more precise data in order to generate reliable predictions (there’s no use in computing the behavior of grid cells that are one meter to a side if we can only resolve/specify real-world states using a grid 1,000 meters to a side).

The link between time-step length and grid size, though, is perhaps slightly less obvious. In general, the shorter the time-steps in the simulation--that is, the smaller Δt is in the difference equations underlying the simulation--the smaller the grid cells must be. This makes sense if we recall that the simulation is supposed to be modeling a physical phenomenon, and is therefore constrained by conditions on the transfer of information between different physical points. After all, the grid must be designed such that during the span between one time-step and the next, no relevant information about the state of the world inside one grid cell could have been communicated to another grid cell. This is a kind of locality condition on climate simulations, and must be in place if we’re to assume that relevant interactions--interactions captured by the simulation, that is--can’t happen at a distance. Though a butterfly’s flapping wings might eventually spawn a hurricane on the other side of the world, they can’t do so instantly: the signal must propagate locally around the globe (or, in the case of the model, across grid cells). This locality condition is usually written:

 ${\displaystyle \Delta t\leq \Delta x/c}$ 6(a)

In the context of climate modeling, ${\displaystyle c}$ refers not to the speed of light in a vacuum, but rather the maximum speed at which information can propagate through the medium being modeled Its value thus is different in atmospheric and oceanic models, but the condition holds in both cases: the timesteps must be short enough that even if it were to propagate at the maximum possible speed, information could not be communicated between one cell and another between one time step and the next.

One consequence of 6(a) is that smaller spatial grids also require shorter time steps. This means that the computational resources required to implement simulations at a constant speed increase not arithmetically, but geometrically as the simulation becomes more precise[7]. Smaller grid cells--and thus more precision--require not just more computation, but also faster computation; the model must generate predictions for the behavior of more cells, and it must do so more frequently[8].

Implementing either an atmospheric or oceanic general circulation model is a careful balancing act between these (and many other) concerns. However, the most sophisticated climate simulations go beyond even these challenges, and seek to couple different fully-fledged circulation models together to generate a comprehensive CGCM.

6.2.1 Coupling General Circulation Models

We can think of CGCMs as being “meta-models” that involve detailed circulation models of the atmosphere and ocean (and, at least sometimes, specialized terrestrial and cryosphere models) being coupled together. While some CGCMs do feature oceanic, atmospheric, cryonic, and terrestrial models that interface directly with one another (e.g. by having computer code in the atmospheric model “call” values of variables in the oceanic model), this direct interfacing is incredibly difficult to implement. Despite superficial similarities in the primitive equations underlying both atmospheric and oceanic models--both are based heavily on fluid dynamics--differences in surface area, mass, specific heat, density, and a myriad of other factors lead to very different responses to environmental inputs. Perhaps most importantly, the ocean and atmosphere have temperature response and equilibrium times that differ by several orders of magnitude. That is, the amount of time that it takes the ocean to respond to a change in the magnitude of some climate forcing (e.g. an increase in insolation, or an increase in the concentration of greenhouse gases) is significantly greater than the amount of time that it takes the atmosphere to respond to the same forcing change. This is fairly intuitive; it takes far more time to heat up a volume of water by a given amount than to heat up the same volume of air by the same amount (as anyone who has attempted to boil a pot of water in his or her oven can verify). This difference in response time means that ocean and atmosphere models which are coupled directly together must incorporate some sort of correction factor, or else run asynchronously most of the time, coupling only occasionally to exchange data at appropriate intervals.[9] Were they to couple directly and constantly, the two models’ outputs would gradually drift apart temporally.

In order to get around this problem, many models incorporate an independent module called a “flux coupler,” which is designed to coordinate the exchange of information between the different models that are being coupled together. The flux coupler is directly analogous to the “orchestra conductor” figure from Richardson’s forecast factory. In just the same way that Richardson’s conductor used colored beams of light to keep the various factory workers synchronized in their work, the flux coupler transforms the data it receives from the component models, implementing an appropriate time-shift to account for differences in response time (and other factors) between the different systems being modeled.

A similarly named (but distinct) process called “flux adjustment” (or “flux correction”) has been traditionally employed to help correct for local (in either the temporal or spatial sense) cyclical variations in the different modeled systems, and thus help ensure that the model’s output doesn’t drift too far away from observation. Seasonal temperature flux is perhaps the most significant and easily-understood divergence for which flux adjustment can compensate. Both the atmosphere and the ocean (at least the upper layer of the ocean) warm during summer months and cool during winter months. In the region known as the interface boundary--the spatial region corresponding to the surface of the ocean, where water and atmosphere meet--both atmospheric and oceanic models generate predictions about the magnitude of this change, and thus the fluctuation in energy in the climate system. Because of the difficulties mentioned above (i.e. differences in response time between seawater and air), these two predictions can come radically uncoupled during the spring and fall when the rate of temperature change is at its largest. Left unchecked, this too can lead to the dynamics of the ocean and atmosphere “drifting” apart, magnifying the error range of predictions generated through direct couplings of the two models. Properly designed, a flux adjustment can “smooth over” these errors by compensating for the difference in response time, thus reducing drift.

6.2.2 Flux Adjustment and “Non-Physical” Modeling Assumptions

Flux adjustment was an early and frequent object of scrutiny by critics of mainstream climatology. The “smoothing over” role of the flux adjustment is frequently seized upon by critics of simulation-based climate science as unscientific or ad-hoc in a problematic way. The NIPCC’s flagship publication criticizing climate science methodology cites Sen Gupta et. al. (2012), who write that “flux adjustments are nonphysical and therefore inherently undesirable... [and] may also fundamentally alter the evolution of a transient climate response.[10]” Even the IPCC’s Fourth Assessment Report acknowledges that flux adjustments are “essentially empirical corrections that could not be justified on physical principles, and that consisted of arbitrary additions of surface fluxes of heat and salinity in order to prevent the drift of the simulated climate away from a realistic state.[11]

What does it mean to say that flux adjustments are “non-physical?” How do we know that such adjustments shift the climate system away from a “realistic state?” It seems that the most plausible answer to this question is that, in contrast to the other components of climate simulations, the flux adjustment fails to correspond directly with quantities in the system being modeled. That is, while the parameters for (say) cloud cover, greenhouse gas concentration, and insolation correspond rather straightforwardly to real aspects of the global climate, the action of the flux adjustment seems more like an ad hoc “fudge factor” with no physical correspondence. The most forceful way of phrasing the concern suggests that by manipulating the parameterization of a flux adjustment, a disingenuous climate modeler might easily craft the output of the model to suit his biases or political agenda.

Is the inclusion of a flux adjustment truly ad hoc, though? Careful consideration of what we’ve seen so far suggests that it is not. Recall the fact that the patterns associated with coarse-grained climate sensitivity have been well-described since (at least) Arrhenius’ work in the late 19th century. Moreover, the advent of quantum mechanics in the 20th century has provided a succinct physical explanation for Arrhenius’ observed patterns (as we saw in Chapter Four). Changes in the concentration of CO2-e greenhouse gases in the Earth’s atmosphere have a deterministic impact on the net change in radiative forcing--an impact that is both well understood and well supported by basic physical theory.

But what of the arguments from Chapter One, Two, and Three about the scale relative behavior of complex systems? Why should we tolerate such an asymmetrical “bottom-up” constraint on the structure of climate models? After all, our entire discussion of dynamical complexity has been predicated on the notion that fundamental physics deserves neither ontological nor methodological primacy over the special sciences. How can we justify this sort of implied primacy for the physics-based patterns of the global climate system?

These questions are, I think, ill-posed. As we saw in Chapter One, there is indeed an important sense in which the laws of physics are fundamental. I argued there that they are fundamental in the sense that they “apply everywhere,” and thus are relevant for generating predictions for how any system will change over time, no matter how the world is “carved up” to define a particular system. At this point, we’re in a position to elaborate on this definition a bit: fundamental physics is fundamental in the sense that it constrains each system’s behavior at all scales of investigation.

6.3.1 Constraints and Models

The multiplicity of interesting (and useful) ways to represent the same system—the fact that precisely the same physical system can be represented in very different state spaces, and that interesting patterns about the time-evolution of that system can be found in each of those state spaces—has tremendous implications. Each of these patterns, of course, represents a constraint on the behavior of the system in question; if some system’s state is evolving in a way that is described by some pattern, then (by definition) its future states are constrained by that pattern. As long as the pattern continues to describe the time-evolution of the system, then states that it can transition into are limited by the presence of the constraints that constitute the pattern. To put the point another way: patterns in the time-evolution of systems just are constraints on the system’s evolution over time.

It’s worth emphasizing that all these constraints can (and to some degree must) apply to all the state spaces in which a particular system can be represented. After all, the choice of a state space in which to represent a system is just a choice of how to describe that system, and so to notice that a system’s behavior is constrained in one space is just to notice that the system’s behavior is constrained period. Of course, it’s not always the case that the introduction of a new constraint at a particular level will result in a new relevant constraint in every other space in which the system can be described. For a basic example, visualize the following scenario.

Suppose we have three parallel Euclidean planes stacked on top of one another, with a rigid rod passing through the three planes perpendicularly (think of three sheets of printer paper stacked, with a pencil poking through the middle of them). If we move the rod along the axis that’s parallel to the planes, we can think of this as representing a toy multi-level system: the rod represents the system’s state; the planes represent the different state-spaces we could use to describe the system’s position (i.e. by specifying its location along each plane). Of course, if the paper is intact, we’d rip the sheets as we dragged the pencil around. Suppose, then, that the rod can only move in areas of each plane that have some special property—suppose that we cut different shapes into each of the sheets of paper, and mandate that the pencil isn’t allowed to tear any of the sheets. The presence of the cut-out sections on each sheet represents the constraints based on the patterns present on the system’s time-evolution in each state-space: the pencil is only allowed in areas where the cut-outs in all three sheets overlap.

Suppose the cut-outs look like this. On the top sheet, almost all of the area is cut away, except for a very small circle near the bottom of the plane. On the middle sheet, the paper is cut away in a shape that looks vaguely like a narrow sine-wave graph extending from one end to another. On the bottom sheet, a large star-shape has been cut out from the middle of the sheet. Which of these is the most restrictive? For most cases, it’s clear that the sine-wave shape is: if the pencil has to move in such a way that it follows the shape of the sine-wave on the middle sheet, there are vast swaths of area in the other two sheets that it just can’t access, no matter whether there’s a cut-out there or not. In fact, just specifying the shape of the cut-outs on two of the three sheets (say, the top and the middle) is sometimes enough to tell us that the restrictions placed on the motion of the pencil by the third sheet will likely be relatively unimportant—the constraints placed on the motion of the pencil by the sine-wave sheet are quite stringent, and those placed on the pencil by the star-shape sheet are (by comparison) quite lax. There are comparatively few ways to craft constraints on the bottom sheet, then, which would result in the middle sheet’s constraints dominating here: most cutouts will be more restrictive than the top sheet and less restrictive than the middle sheet[12]

The lesson here is that while the state of any given system at a particular time has to be consistent with all applicable constraints (even those resulting from patterns in the state-spaces representing the system at very different levels of analysis), it’s not quite right to say that the introduction of a new constraint will always affect constraints acting on the system in all other applicable state spaces. Rather, we should just say that every constraint needs to be taken into account when we’re analyzing the behavior of a system; depending on what collection of constraints apply (and what the system is doing), some may be more relevant than others.

The fact that some systems exhibit interesting patterns at many different levels of analysis—in many different state-spaces—means that some systems operate under far more constraints than others, and that the introduction of the right kind of new constraint can have an effect on the system’s behavior on many different levels.

6.3.2 Approximation and Idealization

The worry is this: we’ve established a compelling argument for why we ought not privilege the patterns identified by physics above the patterns identified by the special sciences. On the other hand, it seems right to say that when the predictions of physics and the predictions of the special sciences come into conflict, the predictions of physics ought to be given primacy at least in some cases. However, it’s that last clause that generates all the problems: if what we’ve said about the mutual constraint (and thus general parity) of fundamental physics and the special sciences is correct, then how can it be the case that the predictions of physics ever deserve primacy? Moreover, how on earth can we decide when the predictions of physics should be able to overrule (or at least outweigh) the predictions of the special sciences? How can we reconcile these two arguments?

Here’s a possible answer: perhaps the putative patterns identified by climate science in this case are approximations or idealizations of some as-yet unidentified real patterns. If this is the case, then we have good reason to think that the patterns described by (for instance) Arrhenius deserve some primacy over the approximated or idealized erstaz patterns employed in the construction of computational models.

What counts as an approximation? What counts as an idealization? Are these the same thing? It’s tempting to think that the two terms are equivalent, and that it’s this unified concept that’s at the root of our difficulty here. However, there’s good reason to think that this assumption is wrong on both counts: there’s a significant difference between approximation and idealization in scientific model building, and neither of those concepts accurately captures the nuances of the problem we’re facing here.

Consider our solar system. As we discussed in Chapter Five, the equations describing how the planets’ positions change over time are technically chaotic. Given the dynamics describing how the positions of the planets evolves, two trajectories through the solar system’s state space that begin arbitrarily close together will diverge exponentially over time. However, as we noted before, just noting that a system’s behavior is chaotic leaves open a number of related questions about how well we can predict its long-term behavior. Among other things, we should also pay attention to the spatio-temporal scales over which we’re trying to generate interesting predictions, as well as our tolerance for certain kinds of error in those predictions. In the case of the solar system, for instance, we’re usually interested in the positions of the planets (and some interplanetary objects like asteroids) on temporal and spatial scales that are relevant to our decidedly humanistic goals. We care where the planets will be over the next few thousand years, and at the most are interested in their very general behavior over times ranging from a few hundred thousand to a few million years (to study the impact of Milankovitch cycles on the global climate, for instance). Similarly, we’re usually perfectly comfortable with predictions that introduce errors of (say) a few thousand kilometers in the position of Mercury in the next century[13]. The fact that we can’t give a reliable prediction about where Mercury will be in its orbit at around the time Sol ceases to be a main-sequence star--or similarly that we can’t give a prediction about Mercury’s position in its orbit in five years that gets things right down to the centimeter--doesn’t really trouble us most of the time. This suggests that we can fruitfully approximate the solar system’s behavior as non-chaotic, given a few specifications about our predictive goals.

Norton (2012) argues that we can leverage this sort of example to generate a robust distinction between approximation and idealization, terms which are often used interchangeably. He defines the difference as follows: “approximations merely describe a target system inexactly” while “[i]dealizations refer to new systems whose properties approximate those of the target system.” Norton argues that the important distinction here is one of reference, with “idealizations...carry[ing] a novel semantic import not carried by approximations.”[14] The distinction between approximation and idealization, on Norton’s view, is that idealization involves the construction of an entirely novel system, which is then studied as a proxy for the actual system of interest. Approximation, on the other hand, involves only particular parameterizations of the target system--parameterizations in which assigned values describe the original system inexactly in some sense.

It’s worth pointing out that Norton’s two definitions will, at least sometimes, exist on a continuum with one another: in some cases, approximations can be smoothly transformed into idealizations.[15]

This interconversion is possible, for instance, in cases where the limits used in constructing idealized parameterizations are “well-behaved” in the sense that the exclusive use of limit quantities in the construction of the idealized system still results in a physically realizable system. This will not always be the case. For example, consider some system ${\displaystyle S}$ whose complete state at a time ${\displaystyle t}$ is described by an equation of the form

 ${\displaystyle S(t)=\alpha ({\tfrac {1}{n}})}$ 6(b)

In this case, both ${\displaystyle \alpha }$ and ${\displaystyle n}$ can be taken as parameterizations of ${\displaystyle S(t)}$. There are a number of approximations we might consider. For instance, we might wonder what happens to ${\displaystyle S(t)}$ as ${\displaystyle \alpha }$ and ${\displaystyle n}$ both approach 0. This yields a prediction that is perfectly mathematically consistent; ${\displaystyle S(t)}$ approaches a real value as both those parameters approach 0. By Norton’s definition this is an approximation of ${\displaystyle S(t)}$, since we’re examining the system’s behavior in a particular limit case.

However, consider the difference between this approximation and the idealization of ${\displaystyle S}$ in which ${\displaystyle \alpha }$ = 0 and ${\displaystyle n}$ = 0. Despite the fact that the approximation yielded by considering the system’s behavior as ${\displaystyle \alpha }$ and ${\displaystyle n}$ both approach 0 is perfectly comprehensible (and hopefully informative as well), actually setting those two values to 0 yields a function value that’s undefined. The limits involved in the creation of the approximation are not “well behaved” in Norton’s sense, and so cannot be used directly to create an idealization. Norton argues that qualitatively similar behavior is common in the physical sciences--that perfectly respectable approximations of a given system frequently fail to neatly correspond to perfectly respectable idealizations of the same system.

Of course, we might wonder what it even means in those cases to say that a given system is an idealization of another system. If idealization involves the genesis of a novel system that can differ not just in parameterization values but in dynamical form the original target system, then how do idealizations represent at all? The transition from an approximation to its target system is clear, as such a transition merely involves reparameterization; the connection between target system and idealization is far more tenuous (if it is even coherent). Given this, it seems that we should prefer (when possible) to work with approximations rather than idealizations. Norton shares this sentiment, arguing that since true idealizations can incorporate “infinite systems” of the type we explored above and “[s]ince an infinite system can carry unexpected and even contradictory properties, [idealization] carries considerably more risk [than approximation]. [...] If idealizations are present, a dominance argument favors their replacement by approximations.”[16]

6.3.3 Idealization and Pragmatism

It’s interesting to note that the examples in Norton (2012) are almost uniformly drawn from physics and statistical mechanics. These cases provide relatively easy backdrops against which to frame the discussion, but it’s not immediately apparent how to apply these lessons to the messier problems in the “high level” special sciences--particularly those concerned with complex systems. Weisberg (2007) suggests a framework that may be more readily applicable to projects like climate modeling. Weisberg discusses a number of different senses of ‘idealization,’ but for our purposes the concept that he calls “multiple-model idealization” (MMI) is the most interesting. Weisberg defines MMI as ”the practice of building multiple related but incompatible models, each of which makes distinct claims about the nature and causal structure giving rise to a phenomenon.”[17] He presents the model building practice of the United States’ National Weather Service (NWS) as a paradigmatic example of day-to-day MMI: the NWS employs a broad family of models that can incorporate radically different assumptions not just about the parameters of the system being modeled, but of the dynamical form being modeled as well.

This pluralistic approach to idealization sidesteps the puzzle we discussed at the close of Section 6.3.2. On Norton’s view, it’s hard to see how idealizations represent in the first place, since the discussion of representation can’t even get off the ground without an articulation of a “target system” and the novel idealized system cooked up to represent it. Weisberg-style pluralistic appeals like MMI are different in subtle but important ways. Weisberg’s own formulation makes reference to a “phenomenon” rather than a “target system:” a semantic difference with deep repercussions. Most importantly, MMI-style approaches to modeling and idealization let us start with a set of predictive and explanatory goals to be realized rather than some putative target system that we may model/approximate/idealize more-or-less perfectly.

By Norton’s own admission, his view of approximation and idealization is one that grounds the distinction firmly in representational content. While this approach to the philosophy of science is the inheritor of a distinguished lineage, the more pragmatically oriented approach sketched by Weisberg is more suitable for understanding contemporary complex systems sciences. As we saw in Section 6.3.2, the question of whether or not a non-chaotic approximation of our solar system’s behavior is a “good” approximation is purpose-relative. There’s no interesting way in which one or another model of the solar system’s long-term behavior is “good” without reference to our predictive goals. Pragmatic idealization lets us start with a goal--a particular prediction, explanation, or decision--and construct models that help us reach that goal. These idealizations are good ones not because they share a particular kind of correspondence with an a priori defined target system, but because they are helpful tools. We will revisit this point in greater detail Section 6.4.2.

6.3.4 Pragmatic Idealization

The solar system, while chaotic, is a system of relatively low dynamical complexity. The advantages of pragmatic MMI-style accounts of idealization over Norton-style hard-nosed realist accounts of idealization become increasingly salient as we consider more dynamically complex systems. Let’s return now to the question that prompted this digression. How can we reconcile a strongly pluralistic view of scientific laws with the assertion that the greenhouse effect’s explanatory grounding in the patterns of physics should give us reason to ascribe a strong anthropogenic component to climate change even in the face of arguments against the veracity of individual computational climate simulations? At the close of Section 6.3.1, I suggested that perhaps the resolution to this question lay in a consideration of the fact that models like the GISS approximate the dynamics of the global climate. In light of the discussion in Sections 6.3.2 and 6.3.3, though, this doesn’t seem quite right. Computational models are not approximations of the global climate in any interesting sense; they are not mere limit-case parameterizations of a single complete model. Neither, though, are they idealizations in Norton’s sense. It seems far more accurate to think of general circulation models (coupled or otherwise) as pragmatic idealizations in the sense described above.

More strongly, this strikes me as the right way to think about climate models in general--as tools crafted for a particular purpose. This lends further credence to the point that I’ve argued for repeatedly here: that the pluralistic and heterogeneous character of the climate model family reflects not a historical accident of development or a temporary waystation on the road to developing One Model to Rule them All. Rather, this pluralism is a natural result of the complexity of the climate system, and of the many fruitful perspectives that we might adopt when studying it.

The project of modeling the global climate in general, then, is a project of pragmatic idealization. The sense of ‘idealization’ here is perhaps somewhere between Weisberg’s and Norton’s. It differs most strongly from Norton’s in the sense that the values of parameters in a pragmatic idealization need not approximate values in the “target system” of the global climate at all. Some apsects of even the best models, in fact, will have explicitly non-physical parameters; this was the worry that kicked off the present discussion to begin with, since it seems that processes like flux adjustment have no direct physical analogues in the global climate itself. Rather, they are artifacts of the particular model--the particular approach to pragmatic idealization--under consideration.

How problematic is it, then, that the flux adjustment has no direct physical analog in the system being modeled? It seems to me that the implication is not so dire as Lupo and Kinimouth make it out to be. This is one sense in which the pragmatic idealization approach shares something in common with Norton’s story--when we create any climate model (but especially a CGCM like the GISS), we have done more than approximate the behavior of the climate system. We’ve created a novel system in its own right: one that we hope we can study as a proxy for the climate itself. The objection that there are aspects of that novel system that have no direct analogue in the global climate itself is as misguided as the objection that no climate model captures every aspect of the climate system. The practice of model building--the practice of pragmatic idealization--involves choices about what to include in any model, how to include it, what to leave out, and how to justify that exclusion. These questions are by no means trivial, but neither are they insurmountable.

6.3.5 Ensemble Modeling and CGCMs

Our discussion so far has focused on the advantages of studying feedback-rich nonlinear systems via computational models: numerical approximation of the solutions to large systems of coupled nonlinear differential equations lets us investigate the global climate in great detail, and through the use of equations derived from well-understood low-level physical principles. However, we have said very little so far about the connection between chaotic behavior and computational modeling. Before we turn to the criticisms of this approach to modeling, let’s say a bit about how simulation is supposed to ameliorate some of the challenges of chaotic dynamics in the climate.

Chaos, recall, involves the exponential divergence of the successors to two initial conditions that are arbitrarily close together in the system’s state space. The connection to climate modeling is straightforward. Given the difficulty--if not impossibility--of measuring the current (not to mention the past) state of the climate with anything even approaching precision, it’s hard to see how we’re justified in endorsing the predictions made by models which are initialized using such error-ridden measurements for their initial conditions. If we want to make accurate predictions about where a chaotic system is going, it seems like we need better measurements--or a better way to generate initial conditions[18].

This is where the discussion of the “predictive horizon” from Section 5.1.3 becomes salient. I argued that chaotic dynamics don’t prevent us from making meaningful predictions in general; rather, they force us to make a choice between precision and time. If we’re willing to accept a certain error range in our predictions, we can make meaningful predictions about the behavior of a system with even a very high maximal Lyapunov exponent out to any arbitrary time.

This foundational observation is implemented in the practice of ensemble modeling. Climatologists don’t examine the predictions generated by computational models in isolation--no single “run” of the model is treated as giving accurate (or even meaningful) output. Rather, model outputs are evaluated as ensembles: collections of dozens (or more) of runs taken as a single unit, and interpreted as defining a range of possible paths that the system might take over the specified time range.

Climate modelers’ focus is so heavily on the creation and interpretation of ensembles that the in most cases CGCMs aren’t even initialized with parameter values drawn from observation of the real climate’s state at the start of the model’s run. Rather, GCMs are allowed to “spin up” to a state that’s qualitatively identical to the state of the global climate at the beginning of the model’s predictive run. Why add this extra layer of complication to the modeling process, rather than just initializing the model with observed values? The spin up approach has a number of advantages; in addition to freeing climate modelers from the impossible task of empirically determining the values of all the parameters needed to run the model, the spin up also serves as a kind of rough test of the proposed dynamics of the model before it’s employed for prediction and ensures that parameter values are tailored for the grid-scale of the individual model.

A typical spin up procedure looks like this. The grid size is defined, and the equations of motion for the atmospheric, oceanic, terrestrial, and cryonic models are input. In essence, this defines a “dark Earth” with land, sky, and water but no exogenous climate forcings. The climate modelers then input relevant insolation parameters--they flip on the sun. This (unsurprisingly) causes a cascade of changes in the previously dark Earth. The model is allowed to run for (in general) a few hundred thousand years of “model time” until it settles down into a relatively stable equilibrium with temperatures, cloud cover, and air circulation patterns that resemble the real climate’s state at the start of the time period under investigation. The fact that the model does settle into such a state is at least a prima facie proof that it’s gotten things relatively right; if the model settled toward a state that looked very little like the state of interest (if it converged on a “snowball Earth” covered in glaciers, for instance), we would take it as evidence that something was very wrong indeed. Once the model has converged on this equilibrium state, modelers can feed in hypothetical parameters and observe the impact. They can change the concentration of greenhouse gases in the atmosphere, for instance, and see what new equilibrium the system moves to (as well as what path it takes to get there). By tinkering with the initial equations of motion (and doing another spin up), the length of the spin-up, and the values of parameters fed in after the spin up, modelers can investigate a variety of different scenarios, time-periods, and assumptions.

The use of spin up and ensemble modeling is designed to smooth over the roughness and error that results from the demonstrably tricky business of simulating the long-term behavior of a large, complex, chaotic system; whether simple numerical approximations of the type discussed above or more sophisticated methods are used, a degree of “drift” in these models is inevitable. Repeated runs of the model for the same time period (and with the same parameters) will invariably produce a variety of predicted future states as the sensitive feedback mechanisms and chaotic dynamics perturb the model’s state in unexpected, path-dependent ways. After a large number of runs, though, a good model’s predictions will sketch out a well-grouped family of predictions--this range of predictions is a concrete application of the prediction horizon discussion from above. Considered as an ensemble, the predictions of a model provide not a precise prediction for the future of the climate, but rather a range of possibilities. This is true in spite of the fact that there will often be significant quantitative differences between the outputs of each model run. To a certain extent, the name of the game is qualitative prediction here.

This is one respect in which the practices of climatology and meteorology have become more unified since Richardson’s and Bjerknes’ day. Meteorologists--who deal with many of the same challenges that climatologists tackle, albeit under different constraints[19]--employ nearly identical ensemble-based approaches to weather modeling and prediction. In both cases, the foundation of the uncertainty terms in the forecast--that is, the grounding of locutions like “there is a 70% chance that it will rain in Manhattan tomorrow” or “there is a 90% chance that the global average temperature will increase by two or more degrees Celsius in the next 20 years”--is in an analysis of the ensemble output. The methods by which the output of different models (as well as different runs of the same model) are concatenated into a single number are worthy of investigation (as well as, perhaps, criticism), but are beyond the scope of this dissertation.

6.4 You Can’t Get Struck By Lightning In a Bottle: Why Trust Simulations?

How do we know that we can trust what these models tell us? After all, computational models are (at least at first glance) very different from standard scientific experiments in a number of different ways. Let us close this chapter with a discussion of the reliability of simulation and computational models in general.

6.4.1 Something Old, Something New

Oreskes (2000) points out that some critics of computational modeling echo a species of hard-line Popperian verificationism. That is, some critics argue that our skepticism about computational models should be grounded in the fact that, contra more standard models, computational models can’t be tested against the world in the right way. They can’t be falsified, as by the time evidence proves them inadequate, they’ll be rendered irrelevant in any case. The kind of parameterization and spin up procedure discussed above can be seen, in this more critical light, as a pernicious practice of curve-fitting: the CGCMs are designed to generate the predictions that they do, as model builders simply adjust them until they give the desired outputs.

However, as Oreskes argues, even the basic situation is more complicated than the naive Popperian view implies: in even uncontroversial cases, the relationship between observation and theory is a nuanced (and often idiosyncratic) one. It’s often non-trivial to decide whether, in light of some new evidence, we ought to discard or merely refine a given model. Oreskes’ discussion cites the problem of the observable parallax for Copernican cosmology and Lord Kelvin’s proposed refutation of old-earth gradualism in geology and biology--which was developed in ignorance of radioactivity as a source of heat energy--as leading cases, but we need not reach so far back in history to see the point. The faster-than-light neutrino anomaly of 2011-2012 is a perfect illustration of the difficulty. In 2011, the OPERA lab at CERN in Geneva announced that it had observed a class of subatomic particles called “neutrinos” moving faster than light. If accurate, this observation would have had an enormous impact on what we thought we knew about physics: light’s role in defining the upper limit of information transmission is a direct consequence of special relativity, and is a direct consequence of geometric features of spacetime defined by general relativity. However, this experimental result was not taken as evidence falsifying either of those theories: it was greeted with (appropriate) skepticism, and subjected to analysis. In the end, the experimenters found that the result was due to a faulty fiber optic cable, which altered the recorded timings by just enough to give a significantly erroneous result.

We might worry even in standard cases, that is, that committed scientists might appropriately take falsifying observations not as evidence that a particular model ought to be abandoned, but just that it ought to be refined. This should be taken not as a criticism of mainstream scientific modeling, but rather as an argument that computational modeling is not (at least in this respect) as distinct from more standardly acceptable cases of scientific modeling DMS might suggest. The legitimacy of CGCMs, from this perspective, stands or falls with the legitimacy of models in the rest of science. Sociological worries about theory-dependence in model design are, while not trivial, at least well-explored in the philosophy of science. There’s no sense in holding computational models to a higher standard than other scientific models. Alan Turing’s seminar 1950 paper on artificial intelligence made a similar observation when considering popular objections to the notion of thinking machines: it is unreasonable to hold a novel proposal to higher standards than already accepted proposals are held to.

We might do better, then, to focus our attention on the respects in which computational models differ from more standard models. Simons and Boschetti (2012) point out that computational models are unusual (in part) in virtue of being irreversible: “Computational models can generally arrive at the same state via many possible sequences of previous states[20].” Just by knowing the output of a particular computational model, in other words, we can’t say for sure what the initial conditions of the model were. This is partially a feature of the predictive horizon discussed in Chapter Five: if model outputs are interpreted in ensemble (and thus seen as “predicting” a range of possible futures), then it’s necessarily true that they’ll be irreversible--at least in an epistemic sense. That’s true in just the same sense that thermodynamic models provide predictions that are “irreversible” to the precise microconditions with which they were initialized. However, the worry that Simons and Boschetti raise should be interpreted as going deeper than this. While we generally assume that the world described by CGCMs is deterministic at the scale of interest--one past state of the climate determines one and only one future state of the climate--CGCMs themselves don’t seem to work this way. In the dynamics of the models, past states underdetermine future states. We might worry that this indicates that the non-physicality that worried Sen Gupta et. al. runs deeper than flux couplers: there’s a fundamental disconnect between the dynamics of computational models and the dynamics of the systems they’re purportedly modeling. Should this give comfort to the proponent of DMS?

6.4.3 Tools for Deciding

This is a problem only if we interpret computational models in general--and CGCMs in particular--as designed to generate positive and specific predictions about the future of the systems they’re modeling. Given what we’ve seen so far about the place of CGCMs in the broader context of climate science, it may be more reasonable to see them as more than representational approximations of the global climate, or even as simple prediction generating machines. While the purpose of science in general is (as we saw in Chapter One) to generate predictions in how the world will change over time, the contribution of individual models and theories need not be so simple.

The sort of skeptical arguments we discussed in Section 6.4.2 can’t even get off the ground if we see CGCMs (and similar high-level computational models) not as isolated prediction-generating tools, but rather tools of a different sort: contextually-embedded tools designed to help us figure out what to do. On this view, computational models work as (to modify a turn of phrase from Dennett [2000]) tools for deciding.[21] Recall the discussions of pragmatic idealization and ensemble modeling earlier in this chapter. I argued that CGCMs are not even intended to either approximately represent the global climate or to produce precise predictions about the future of climate systems. Rather, they’re designed to carve out a range of possible paths that the climate might take, given a particular set of constraints and assumptions. We might take this two ways: as either a positive prediction about what the climate will do, or as a negative prediction about what it won’t do.

This may seem trivial to the point of being tautological, but the two interpretations suggest very different roles for pragmatic idealization generally (and CGCMs in particular) to play in the larger context of climate-relevant socio-political decision making. If we interpret CGCMs as generating information about paths the global climate won’t take, we can capitalize on their unique virtues and also avoid skepical criticisms entirely. On this view, one major role for CGCMs’ in the context of climate science (and climate science policy) as a whole is to proscribe the field of investigation and focus our attention on proposals worthy of deeper consideration. Knowledge of the avenues we can safely ignore is just as important to our decision making as knowledge of the details of any particular avenue, after all.

I should emphasize again that this perspective also explains the tendency, discussed in Chapter Four, of progress in climatology to involve increasing model pluralism rather than convergence on any specific model. I argued there that EMICs are properly seen as specialized tools designed to investigate very different phenomena; this argument is an extension of that position to cover CGCMs as well. Rather than seeing CGCMs as the apotheosis of climate modeling--and seeking to improve on them to the exclusion of other models--we should understand them in the context of the broader practice of climatology, and investigate what unique qualities they bring to the table.

This is a strong argument in favor of ineliminable pluralism in climatology, as supported by Parker (2006), Lenhard & Winsberg (2010), Rotmans & van Asselt (2001), and many others. I claim that the root of this deep pluralism is the dynamical complexity of the climate system, a feature which necessitates the kind of multifarious exploration that’s only possible with the sort of model hierarchy discussed in Chapter Four. Under this scheme, each model is understood as a specialized tool, explicitly designed to investigate the dynamics of a particular system operating under certain constraints. High-level general circulation models are designed to coordinate this focused investigation by concatenating, synthesizing, and constraining the broad spectrum of data collected by those models. Just as in the scientific project as a whole, “fundamentalism” is a mistake: there’s room for a spectrum of different mutually-supporting contributions

1. The term “coupled general circulation models” is also occasionally used in the literature. The two terms are generally equivalent, at least for our purposes here.
2. At the time when Richardson wrote this passage, the word ‘computer’ referred not to a digital computer--a machine--but rather to a human worker whose job it was to compute the solution to some mathematical problem. These human computers were frequently employed by those looking to forecast the weather (among other things) well into the 20th century, and were only supplanted by the ancestors of modern digital computers after the advent of punch card programming near the end of World War II.
3. Here, Richardson is describing the now well-respected (but then almost unheard of) practice of studying what might be called “homologous models” in order to facilitate some difficult piece of computation. For example, Bringsjord and Taylor (2004) propose that observation of the behavior of soap bubbles under certain conditions might yield greater understanding of the Steiner tree problem in graph theory. The proposal revolves around the fact that soap bubbles, in order to maintain cohesion, rapid relax their shapes toward a state where surface energy (and thus area) is minimized. There are certain structural similarities between the search for this optimal low-energy state and the search for the shortest-length graph in the Steiner tree problem. Similarly, Jones and Adamatzsky (2013) show slime molds’ growth and foraging networks show a strong preference for path-length optimization, a feature that can be used to compute a fairly elegant solution to the Traveling Salesman problem.
4. Image by Francois Schuiten, drawn from Edwards (2010), p. 96
5. Edwards (2010), pp. 93-98
6. Ibid., p. 178
7. In practice, halving the grid size does far more than double the computational resources necessary to run the model at the same speed. Recall that in each grid, at least six distinct variables are being computed across three dimensions, and that doubling the number of cells doubles the number of each of these calculations.
8. Of course, another option is to reduce the output speed of the model--that is, to reduce the ratio of “modeled time” to “model time.” Even a fairly low-power computer can render the output of a small grid / short time step model given enough time to run. At a certain point, the model output becomes useless; a perfect simulation of the next decade of the global climate isn’t much use if it takes several centuries to output.
9. McGuffie and Anderson-Sellers (2010), p. 204-205
10. Sen Gupta et. al. (2012), p. 4622, quoted in Lupo and Kininmonth and (2013), p. 19
11. IPCC AR4: 1.5.3
12. Terrance Deacon (2012)’s discussion of emergence and constraint is marred by this confusion, as he suggests that constraints in the sense of interest to us here just are boundary conditions under which the system operates.
13. Of course, there are situations in which we might demand significantly more accurate predictions than this. After all, the difference between an asteroid slamming into Manhattan and drifting harmlessly by Earth is one of only a few thousand kilometers!
14. Norton (2012), pp. 207-208
15. Norton (2012), p. 212
16. Norton (2012), p. 227
17. Weisberg (2007), p. 647
18. This problem is compounded by the fact that we often want to initialize climate models to begin simulating the behavior of the climate at times far before comprehensive measurements of any kind--let alone reliable measurements--are available. While we can get some limited information about the climate of the past through certain “proxy indicators” (see Michael Mann’s work with glacial air bubbles, for instance), these proxy indicators are blunt tools at best, and are not available at all for some time periods.
19. This too is a practical illustration of the concept of the predictive horizon. Weather prediction must be far more precise than climate prediction in order to be interesting. However, it also need only apply to a timeframe that is many, many order of magnitude shorter than climate predictions. Meteorologists are interested in predicting with relatively high accuracy whether or not it will rain on the day after tomorrow. Climatologists are interested in predicting--with roughly the same degree of accuracy--whether or not average precipitation will have increased in 100 years. The trade-off between immediacy and precision in forecasting the future of chaotic systems is perfectly illustrated in this distinction.
20. Simons and Boschetti (2012), p. 810
21. This view is not entirely at odds with mainstream contemporary philosophy of science, which has become increasingly comfortable treating models as a species of artifacts. van Fraassen (2009) is perhaps the mainstream flagship of this nascent technological view of models.