American Scientist

The Ozone Layer: A Philosophy of Science Perspective. Maureen Christie. xii + 215 pp. Cambridge University Press, 2000; first published in 2001. $64.95 cloth; $22.95 paper.

Maureen Christie's carefully reasoned book presents a critical philosophical analysis of the evidence developed between 1970 and 1994 on the effects of human-produced chlorinated fluorocarbons (CFCs) on the ozone layer. She aims to show why standard accounts of evidence within the philosophy of science cannot do justice to this episode in atmospheric science and proposes alternatives to the standard accounts. In this she is remarkably successful, providing an illuminating way to understand the interplay of argument and evidence. Because disputes over the strength of evidence in environmental science are becoming central to issues in social and legislative policy, her analysis is important to a wide audience.

Part I of The Ozone Layer relates the history of our understanding of stratospheric ozone. The story begins with the recognition of ozone in the upper atmosphere in 1879, which was followed by the realization that ozone shields the surface of the Earth from ultraviolet radiation. In the 1920s emerged the general outline of a chemistry that explains why ozone is present in quantity only in an altitude range of 15 to 50 kilometers and why it exhibits patterns of annual variation. Then, beginning in the 1930s, CFCs were produced as an ideal nontoxic, unreactive refrigerant—which unfortunately, due to its inertness, accumulates in the stratosphere. In the 1960s, the possibility was raised that human activity might compromise the ozone layer (the concern then was not CFCs, but high-altitude flights).

In the early 1970s, Mario J. Molina and F. Sherwood Rowland identified a sequence of chemical reactions by which CFCs could gradually deplete the ozone layer. In the mid-1980s, investigators discovered that an ozone "hole" had developed over the Antarctic each spring for the past decade and that the hole was increasing in size.

The chemistry proposed by Molina and Rowland, for which they won the Nobel Prize in 1995, required ultraviolet radiation. Their original computer modeling suggested that CFCs had caused about a 5 percent general depletion of the ozone layer globally, and various models based on their work built by others in the early 1980s showed much smaller effects. So the appearance of an ozone hole in the Antarctic in the spring, given that ultraviolet radiation at the poles in the winter and early spring is very low, was inconsistent with the Molina-Rowland chemistry, as were the very high seasonal depletions of ozone (of up to 60 percent) that were observed in the Antarctic. Three conflicting speculative approaches emerged to finding an explanation for the Antarctic ozone hole: Atmospheric chemists looked to variants of the Molina-Rowland chemistry; meteorologists proposed that the hole resulted from a change in patterns of air circulation; and others, primarily atmospheric physicists, attributed the hole to an increase in solar activity from 1975 to 1980, which resulted in a much higher seasonal concentration of ozone-depleting oxides of nitrogen over the Antarctic.

In the late 1980s, a highly organized effort to gain data (the Antarctic Airborne Ozone Experiment) revealed, among other things, a systematic reverse correlation between the concentrations of chlorine monoxide (ClO) and ozone (O₃) in the stratosphere at high southern latitudes in the spring. This finding was a "smoking gun," producing a rapid consensus that the culprit was chlorine and hence CFCs. After that, efforts focused on understanding the detailed chemistry involved. Christie ends her history in 1994. By then, much of the chemistry had been identified, but the process of elaborating it continues.

In Part II (the bulk of the book), Christie draws out philosophical implications from these events. The heart of the book consists of discussions of the role of prediction, the logical force of "crucial experiments," and the asymmetry in logic between observations that support and observations that falsify a theory. She also considers the issue of communication among subdisciplines of science, concluding that communication difficulties among groups of researchers occurred in much the way that Thomas Kuhn and others have asserted; although these were not insurmountable, cross-disciplinary communication emerged only in the very late stages of investigation. The book ends with a critical examination of claims that the evidence for ozone depletion is insufficient to warrant action against CFCs.

Christie identifies two types of prediction in science. In one, claims are deduced from a theory in order to test it; in the other, prediction aims to foretell the future behavior of a natural system. (Christie uses the term prophecy for the latter, to capture its practical importance and the potential difficulties that surround it.) Molina and Rowland's original system could be seen as having fared poorly on both counts. Its predicted level of global ozone depletion was excessive; and it considered only ultraviolet light and gaseous chemistry, whereas the Antarctic "hole" arises from visible light and chemistry acting on the surface of the ice crystals in polar stratospheric clouds, which are made up of water and nitric acid. Molina and Rowland had no way to anticipate the huge ozone depletion that began to occur seasonally over the Antarctic shortly after their work was published.

Despite the failures of Molina and Rowland's original system, scientists whom Christie interviewed regarded their theory not as false, but only as incomplete—for the principal reactions singled out by Molina and Rowland remain part of the story. The two men were indeed instrumental in focusing research on CFCs.

Christie accordingly maintains that the actual workings of prediction in science are much more complicated and subtle than standard accounts would have it. In particular, she argues, a distinction is needed between failures of prediction that call for the unqualified rejection of a theory and those that call for a theory to be fine-tuned. The difference turns on whether the overall pattern of predictive behavior indicates that modification and extension of the theory is more promising than its wholesale abandonment.

Christie also takes on the question of crucial experiments, convincingly demonstrating that discovery of the reverse correlation between ClO and O₃ marked a turning point in research into the ozone hole. Afterward, most work on chemistry-free air-circulation alternatives ceased. Yet the "smoking gun" evidence did not falsify those alternatives, nor was it an unavoidable implication of every chemical theory.

In Christie's words, there was no specific commitment "to a necessity that elevated ClO should be both observable and observed, and that the chlorine theories should stand or fall on whether it was." So why did the alternatives to chlorine chemistry disappear so rapidly and so thoroughly? Because, Christie argues, amid otherwise highly irregular data, the tight fit between falling ozone and rising ClO levels provided strong evidence of a causal link between the two. If ClO levels had instead risen smoothly with latitude, and ozone levels had reciprocally fallen smoothly, the evidence for a causal link from these data alone would have been less compelling than it was. The chlorine theories did not imply such a fit as a necessary result. Rather, because this unexpected tight fit gave strong reason to think that chlorine mechanisms are critically implicated in the causal sequence, it turned research quickly in their direction, deflecting it from others that now seemed less promising. The research problem became the more focused one of filling out the causal sequence—identifying the other, complementary factors responsible for the annual springtime ozone hole over the Antarctic. Christie concludes that the effect of the ClO-O₃ "smoking gun" is therefore best viewed as an instance of Francis Bacon's notion of a crucial experiment as a "fingerpost at the crossroads": Go this way, not that, and fruitful research will be your reward.

Karl Popper long ago argued that empirical observations can never truly confirm a theory, they can only falsify or fail to falsify it. Yet the ClO-O₃ reciprocity appears to do nothing but provide supportive evidence for some chlorine chemistry mechanism. In response to this apparent difficulty, Christie offers a way of bringing falsification into play. Every theory, she says, has an antithesis—a theory that is in some way its direct opposite. For the theory that chlorine chemistry plays a central causal role in the ozone hole, the antithesis is that it doesn't. A theory can be confirmed by falsification of its antithesis, and, Christie concludes, this is the proper way to view the logical force of the reverse correlation between ClO and O₃.

This might seem to be a mere playing with words in order to rescue falsification for this type of science, but it isn't. Large-scale, multifactor natural systems (at least) require a brand of philosophy that can take account of the fact that the system as a whole cannot be properly modeled in the laboratory, nor can all of the relevant factors and their mutual interactions be thoroughly specified in advance. Although the last point certainly holds for many, if not most, laboratory systems, nevertheless there is a signal difference: These sorts of natural systems are not subject to experimental control—they cannot be altered to test this or that idea about what factors are relevant. Data gathering accordingly becomes a considerably different affair, subject much more to the whim of unalterable and even uncontrollable circumstance than are most laboratory investigations. But even laboratory investigations, we would argue, exhibit behavior that deviates considerably from standard views concerning the role of theory.

Christie assumes that the sole purpose of theory is to explain phenomena, whether in nature or in a laboratory. Yet theory often functions primarily as a tool in ongoing research. Especially in the early stages of theory construction, a theoretical fragment may be put forward with the hope that observed deviations from predictions derived from this fragment will reveal how to modify and extend it.

Christie points out that the principal falsehood in Molina and Rowland's original theory was their claim that no other chemical mechanisms have significant effects. One could lodge the same criticism of 18th- and early 19th-century figures working out the details of planetary motions: Their calculations all assumed that the only forces at work were the gravitational forces toward the Sun and the seven known planets and their satellites. The deviation of Uranus from these calculations led to the discovery of Neptune in much the same way that the failure of Molina and Rowland's system to yield anything like the Antarctic ozone hole led to the recognition of complementary chemical mechanisms that did.

The most fruitful way to play with the behavior of large-scale natural systems such as atmospheric chemistry or planetary motions is to model them on a computer. Natural systems that are not multifactor systems (planetary motions are determined entirely by gravity) can often be modeled for periods of time that have human significance. The solar system is computationally stable for periods on the order of tens of thousands of years; gas-flow dynamics has computational stability for periods of the order of fractions of a second, but this (together with averaging) is often sufficiently long to derive useful information. Multifactor systems may in general not be computationally tractable in a similarly useful way, even when the goal is to provide information about large-scale behavior, such as the formation of the ozone hole.

Christie, although she does not comment directly on this difference, nevertheless raises it implicitly when she asks how a computer model can be part of empirical research when so many of its features have to be stipulated, with computational considerations often dictating choices. Here, we would argue, it is again a question of promise in the light of available evidence: Observed deviations from the behavior predicted by the models may exhibit patterns that point the way toward improvements. As Christie says, the crucial question is whether the deviations are systematic in an instructive way, for then empirical results can at one and the same time be evidence not only that the existing theory is false, but also that it is highly promising. There are dangers here as well, because, as Christie points out, the model can easily become an end in itself, and data that do not fit the model's inherent demands may be ignored or overlooked. Given the contemporary importance of computer simulation, this topic deserves further pursuit.

Recognizing that theory can have the short-term goal of furthering research introduces a major complication when assessing the quality of evidence. To claim that the evidence for something—Maxwell's electrodynamic equations or fundamental theory in chemistry, for example—is very strong is tantamount to saying that the elaborate theoretical frameworks developed out of it cover a huge range of details to very high precision. This is the sense of strong evidence for completed theories that has dominated standard philosophy of science. By contrast, in the early stages of theory construction the strength of the evidence supporting a fragment of a theory turns on how unequivocally it points the way toward modifications and extensions. Although Christie does not use our terminology, this is precisely what she concludes when she says that the "smoking gun" was overwhelming evidence for the promise of chlorine-based mechanisms. Of course, writing in the late 1990s, she has the advantage of hindsight. Confusion arises when scientists, and others, talk of strong evidence for a theory without paying attention to the contrast between the early stages of theory construction and comparatively finished science.

Unnuanced talk about the strength of evidence can have pragmatically unfortunate consequences. The shrinking ozone layer after all may have, or be symptomatic of, drastic ecological consequences. Policy must be developed and decisions made; risks must be balanced against potential gains. Science can often shed light on the likelihood of risk and gain, but not always with the unbreakable certainty that policy makers might wish, because many questions call for decisions that cannot wait until a more finished scientific scheme is in place. In the case of aircraft failures, for example, even the total absence of evidence that some particular factor did not cause an airplane to crash—in other words, a total inability to eliminate that factor—can be sufficient reason to warrant doing something to safeguard against its causing a future crash. Standards of evidence when risk is central can be very different from standards of evidence in either comparatively finished science or science in the early stages of theory construction.

These differing standards can be a serious source of continuing confusion in disputes over such matters as ozone depletion. Indeed, they clearly have been so in respect to global warming. A consensus among scientists can form because the evidence strongly supports the promise of a theory. Those who think that their vested interests may be adversely affected by policies based on this evidence can always invoke the standard of finished science to argue for delay. And all the while the policy question is best viewed as a balance of risks against gains, given currently available information. The great value of Christie's book is the step she has taken toward making all this very clear indeed.