Why trust science?

Naomi Oreskes’s recent book, Why Trust Science?, occupies an underpopulated space: It is interesting to an audience of professional historians or philosophers of science, but it also aims to engage a much larger part of the public. The book is motivated by Oreskes’s work on climate change denialism, and it asks: Why should we trust the pronouncements of scientists?

Oreskes begins by rejecting the view that scientists employ special methods by which they are able to tell what is true. We might think that scientists only hold theories that have been appropriately verified. But no: Philosophers have long argued, for a variety of reasons, that we can never verify theories in the sense of conclusively demonstrating their truth. Or perhaps proper scientific theories must be falsifiable, and must have survived many rigorous attempts at falsification? Again, this famous proposal by Karl Popper did not hold up to scrutiny. Oreskes goes through additional suggestions, and many influential philosophers make an appearance: Comte, Duhem, Hempel, Quine, Kuhn — and of course Feyerabend, who wrote “against method”.

Oreskes argues that scientific method ultimately cannot be what guarantees the trustworthiness of scientific findings. Instead, she suggests that we should look to social aspects of science. For example, we should ask whether the relevant scientific community is diverse, so that many viewpoints are represented. And we should ask whether the community allows critical discussion, so that superior viewpoints have a chance to prevail. In brief, our trust in science ought to rest not on truth-conducive methods, but on a truth-conducive type of social organisation. If an appropriately open, diverse, and critical scientific community reaches a consensus on a question, that consensus can probably be trusted. Since we cannot know for sure what is true, we use consensus as a proxy.

This is an appealing solution to the problem, and I have no doubt that it gets at something important. However, I am not convinced that it can successfully bracket the question of method. Here’s why. For group consensus to be a meaningful proxy for truth, we have to assume that the group can somehow assess whether its methods a truth-tropic, that is, whether they are sensitive to how the world actually is (which is not to say that these methods are required to be infallible). We must also assume that such an assessment of truth-tropism is relevant to the emergence of consensus. Otherwise the consensus might indicate nothing more than that the entire community has convinced itself to use the same, although unreliable, methods. If a community lacks methods that are truth-tropic, or lacks the ability to tell which of its methods are truth-tropic, or does not care, then its consensus doesn’t count for much — even if the community is wonderfully diverse, open, and critical.

Oreskes rightly fears that strong methodological norms could become a straightjacket (she speaks of a “fetish”), such as when we demand randomised, controlled trials in cases where they are neither feasible nor necessary. She discusses, for example, the debates about the effectiveness of dental flossing. Even in the absence of RCTs, she argues, we should not dismiss the abundant mechanistic evidence that flossing is effective against periodontal disease. I agree! However, this does not show that methodological norms are a bad thing to have. It only shows that we should not adopt artificially narrow accounts. The goal of scientific epistemology must be to study the full range of methods that empirical scientists employ, and to learn about their track records as epistemic tools.

To be clear, I think that we should in most cases trust science. I also think that the social organisation of scientific inquiry is important and deserves much more attention from philosophers of science than it has so far received. And, finally, I agree with Oreskes that the existence of a consensus within a scientific community is an important indicator of whether any particular scientific result ought to be trusted. Consensus is an especially important indicator for a general, non-expert public. But as historians and philosophers of science, we have an additional explanatory aim. It is to understand why consensus in a community can be taken as an indication that particular claims are likely to be true. And this requires a debate about the methods by which such claims are assessed, even if we believe that this assessment is a social processs.

(P.S.: I often dabble in the debates about what, if anything, the history of science and the philosophy of science have to learn from each other. Oreskes’s book is interesting in this respect. She clearly self-identifies as a historian of science. But in this book she begins by reviewing philosophical accounts of method, and she returns to this philosophical framing throughout as she discusses episodes from the history of science. I think that this is not at all surprising: If the epistemology of science is our interest, then we are in an area where the history and the philosophy of science naturally intersect.)

Science and the English language

My attention was drawn to an editorial in Nature about the phrase “necessary and sufficient” in neuroscience papers (via @sophiejveigl): 

If a gene is necessary and sufficient for something (as often claimed), strict logic demands that that gene alone can do the job. For example, the gene eyeless is certainly necessary for a retina to develop. But it is not sufficient — if it were, then logic would demand that ‘if eyeless exists, then a retina will develop’. This is false; other genes and factors are needed as well. Yet eyeless is often described as being necessary and sufficient for retinal development.

The suggestion discussed in the editorial is that genes should instead be called “indispensable and inducing”. This is sensible as far as it goes, since the connotation of “inducing” is that the gene causes the expression of the trait, but that it does not do so invariably — only in appropriate background circumstances, that is, in conjunction with a set of further genes and other relevant conditions. “Indispensable” captures the methodological strategy that the relationship between a gene and a trait is demonstrated by suppressing the gene in a controlled experiment, to see whether the trait disappears as well.

But why not just say that “the gene causes the expression of the trait”? I am not aware of any influential analysis of causation that suggests that causes are individually sufficient. For my part, I think that the INUS analysis is quite handy for everyday occasions (I teach it to students of biology and medicine). On the INUS analysis, a cause is an Insufficient but Necessary part of a condition that is Unnecessary but Sufficient for an effect.

This is a mouthful, but easy to understand by example. Aspirin, in suitable background circumstances, relieves headaches. (It is individually insufficient for the effect, but a necessary part of a jointly sufficient condition.) But other interventions (a warm bath) can also relieve headaches within their own sufficient set of circumstances. (So each sufficient set of circumstances is individually unnecessary.)

So you see, editors of Nature, you already have le mot juste. It is the humble “causes”. Why would this not serve biologists well?

Review: Jutta Schickore, “About Method” (University of Chicago Press, 2017)

(This is a significantly expanded version of my review for NTM Journal of the History of Science, Technology and Medicine, which will appear later this year.)

Jutta Schickore’s About Method focuses on a neglected genre of scientific texts: what she calls the “methods discourse” of experimentalists. She argues that even though the philosophical and historical literature on experimental science is vast, little attention has been paid to what scientists themselves have to say about how to design, evaluate, and report the results of experiments. She acknowledges, of course, that methods discourse may be an unreliable guide to what scientists actually do in experimental practice, but she argues that it nevertheless offers a unique window into scientists’ conceptions of proper experimental procedure.

The book is structured around an extended case study of research on snake venom. This is a felicitous choice. It allows Schickore to connect significant episodes in the history of experimentation ranging from seventeenth-century Europe to the late nineteenth-century United States. We meet Francesco Redi (1626—1697), the Italian physician and naturalist who is now best known for his experiments questioning spontaneous generation. In his treatise on vipers, he insisted on repeating experiments many times in order to show that the “yellow liquor” in vipers’ teeth caused poisoning if it was inserted into wounds, but not if it was swallowed. Two chapters focus on Felice Fontana (1730—1805), who has been lauded as one of the first experimentalists to use adequate controls. Working a century after Redi, Fontana relied on the variation of experimental circumstances to determine which tissues snake venom acts upon. Another century later, the American physician Silas Weir Mitchell (1829—1914), among others, sought to isolate the active components in snake venom. Schickore finally links the research on snake venom to broader nineteenth-century reflections on the nature and limits of experimental inquiry, especially through the widely felt influence of the French physiologist and methodologist Claude Bernard (1813—1878). As we travel along this historical arc, the stability of snake venom as a research problem serves as a backdrop against which we recognize the evolution of experimental methods.

Schickore distinguishes multiple layers of methods discourse. At an extreme level of generality, we find scientists making broad commitments: for example, that experience is the only path to certain knowledge. At the other extreme, we find detailed discussions of particular laboratory procedures: of how precisely an incision was made and poison was deposited. Schickore, however, focuses on an intermediate level: that of methodological strategies and principles, such as the notions that we should conduct comparative experiments, repeat them, and vary their circumstances. Intriguingly, this intermediate level of analysis reveals continuities between researchers and time periods that remain hidden at the level of broad commitments or concrete research practices.

To illustrate, consider the contrast between two nineteenth-century scientists and methodologists, John Herschel and Claude Bernard. Herschel’s broad commitment was to a form of Baconianism, and his experience with experimental practice was in the physical sciences. Bernard, by contrast, could never quite stop kicking Bacon in the shins, as it were, and his practical experience was in physiology. Nevertheless, at the intermediate level of methodological strategies there was much that united the two. Both, for example, were interested in the theory and epistemic force of comparative experimentation. Thus, the middle-level analysis permits us to recognize significant continuities that might otherwise remain hidden.

Scholars have often reinterpreted methodological statements as efforts at positioning and persuasion, but Schickore believes a literal reading is often appropriate. For example, Redi’s emphasis of his many resource-consuming repetitions has been seen as a “political gambit to display the power of the Tuscan court” (32). However, organisms are highly variable, and repeating experiments helps to reveal variations and to discover which findings are reliable. Schickore shows that Redi defended his methodological views on such epistemic grounds. We have read much about the ways in which detailed descriptions of experimental procedures served to establish an experimenter’s credibility. Schickore, by contrast, emphasizes the role of methodological statements in establishing the credibility of the experimental procedures themselves.

About Method highlights the power of Schickore’s approach to integrated history and philosophy of science. She has previously argued that in order to understand current concepts and practices, we must often study how these concepts and practices have come into existence. The case of experimental method is an excellent example. Present-day methodological statements are all about the particulars of experimental processes and rarely discuss underlying methodological principles. There is much that we have simply come to take for granted. To understand the epistemic aims of such practices as comparisons, repetitions, and variations, we must look to a time when these practices were still controversial and needed explicit defense.

In some instances, it would have been welcome to drive the analysis further. For example, I would have liked to see how precisely Redi or Fontana deployed strategies like repetitions or variations of circumstances, and what inferences these strategies enabled. It is one thing to say that repetitions or variations reveal sources of error — but how did this work in concrete cases? Perhaps such an analysis would have seemed to Schickore too much like an attempt to “measure the distance” (9) between historical actors and modern-day conceptions of experimental reasoning. Or perhaps the shift from methods discourse to practice would have meant a loss of focus. In any case, I would have like to read more about the nitty-gritty details of experimental reasoning.

The title of Schickore’s book is a play on Paul Feyerabend’s seminal Against Method, which was published in 1975. It is telling that the method that Feyerabend argued against has very little in common with the methods that Schickore’s historical actors write about. The goal of the snake venom researchers was to isolate suspected causes, and to demonstrate their competence to produce the effects ascribed to them. These researchers worried about targeted interventions and the control of confounding variables, not about the power of falsification and the problems of ad hoc hypotheses. Schickore’s title is thus fitting. Her book is in many ways orthogonal to older debates. It is not a counterweight to Feyerabend’s book: for method, a defense of a philosophical project. It is about method: a description, an analysis, an invitation to a new dialogue.

To conclude, About Method is an excellent book. It not only gives us insights into the long-term development of experimental methods, but also serves as a model of how to conduct studies at the interface of history and philosophy of science.

Worn passports

Vladimir Nabokov would probably have produced some nice work in integrated history and philosophy of science:

In art as in science there is no delight without the detail, and it is on details that I have tried to fix the reader’s attention. Let me repeat that unless these are thoroughly understood and remembered, all “general ideas” (so easily acquired, so profitably resold) must necessarily remain but worn passports allowing their bearers short cuts from one area of ignorance to another.

The emphasis is mine.

Do biologists infer to the best explanation?

The modern debate about scientific realism is to a large extent a debate about the reliability of inference to the best explanation (IBE). Proponents of anti-realism argue that IBE is inherently problematic. We cannot expect it to lead us to true theories, since it only picks the best of the available hypotheses, leaving us susceptible to unconceived alternatives. Newtonian physics was certainly a powerful explanation — until a patent clerk in Bern conceived a superior alternative, special relativity. Realists in turn defend IBE, arguing, for example, that IBE has become more powerful over time because the scientific community has grown; or that those parts of theories that fuel their explanatory success have actually proved stable over time; or that explanatory theories are strongly confirmed only if they made novel predictions.

In a forthcoming paper co-authored with Aaron Novick, we approach this debate in a different way. We concede that IBE is a dangerous method, just as anti-realists have argued. But biologists already recognize its dangers and insist on more stringent methodological standards before they accept hypotheses as established. Explanatory power is not enough. We propose that biologists instead adhere to versions of the vera causa standard. It requires that causes be shown to exist, to be competent to produce the kinds of effects ascribed to them, and to be responsible for particular instances of those effects. Until this standard has been met, the biological community accepts causal claims only provisionally, regardless of how powerfully they explain. We support this thesis by studying debates about the physical basis of heredity from the late 19th century (when multiple ingenious hypotheses failed) to the early 20th century (when Mendelian genes were localized to chromosomes) and finally to the middle of the 20th century (when DNA was shown to transmit at least some heritable traits). While explanatory power certainly served as a guide to the “pursuitworthiness” of hypotheses, it played little or no role in their acceptance. We thus de-emphasize the importance of explanatory power and emphasize instead the importance of detection and intervention, and of inferring causal competence by various experimental and observational methods. On this basis, we develop a new case for scientific realism about many (not all) claims in biology.

One distinction is crucial in this debate. We do not deny that scientific activity is often bound up with explanation. Once scientists have inferred the truth or likely truth of a hypothesis, they use that hypothesis in order to explain things. But IBE postulates something more: that we infer the truth or likely truth of hypotheses because they explain. This is where we disagree: Biologists seem to ask much more of their hypotheses.

The paper is titled “Presume it not: True causes in the search for the basis of heredity”. It is forthcoming in the British Journal for the Philosophy of Science, and a preprint is now available on the PhilSci archive. I like how this one turned out.

Difficulties and Intricacies of Creating and Using Historical Case Studies

Joseph Pitt has written a review for Metascience of our Boston Studies volume on The Philosophy of Historical Case Studies. We appreciate his generally positive tone. I think he is correct that our title overpromises: it would have been more accurate, as he suggests, to title the volume Difficulties and Intricacies of Creating and Using Historical Case Studies. But there must be some concessions to catchiness.

My contribution with Tim Räz gets a few kind words:

What is rewarding in the approach Scholi and Räz develop is its nuanced appreciation of the intricate dance that history and philosophy engage in as they support and confront each other.

That’s not how I usually spell my name, but you take the bitter with the better.

“Words, words, words, I’m so sick of words!”

Many scientists seem to agree with a favorite adage of the best film directors: “show, don’t tell”. A look at the latest articles in Nature will often reveal that half of the available space is devoted to pictures and diagrams rather than text. Supplemental materials may even consist exclusively or almost exclusively of diagrams.

While historians of science have long paid attention to visual representations, philosophers have by and large ignored them. But this is slowly beginning to change. In the last decade or so there have been recurrent bubbles of philosophical interest in diagrams, including a project directed by William Bechtel and Adele Abrahamsen at UCSD under the lovely acronym Worgods (Working Group on Diagrams in Science). While I was at the Pittsburgh Center with the two of them, I quickly recognized not only how important diagrams are in scientific practice, but also that they had figured prominently in much of my previous research. I had just never stopped to consider them as objects of inquiry in their own right.

Take this diagram as an example:

Spot the difference figures
A figure from Fire et al. in Nature, 1998, volume 391, p. 808.

The figure appeared in a 1998 paper in Nature by Fire et al. It shows fluorescence micrographs of green fluorescent protein (GFP) in C. elegans. In a and b, GFP is expressed in a larva and in an adult, respectively. In d and e, the expression is suppressed. In g and h, the expression of GFP targeted to the nucleus is suppressed, but not the expression of GFP targeted to mitochondria. What is the point of figures like this one? In a forthcoming paper, I give a pretty straightforward answer. Many of the diagrams in your routine scientific publication depict what I call “causal contrasts”. They show what happens to a particular outcome variable if a specific intervention is performed, comparing this to a control in which the intervention is not performed. In the diagram above, the point is to show that an intervention with double-stranded RNA can suppress the expression of sequence-homologous genes (compare a and d, b and e). What is more, the diagram shows the specificity of this effect: if the double-stranded RNA is targeted only against the nuclear GFP gene, then the expression of mitochondrial GFP remains unaffected (compare a and g, b and h). For their demonstration of this extremely effective technique for gene suppression, the authors received the 2006 Nobel Prize in physiology or medicine.

I argue in the paper that many diagrams show causal contrasts, even though they differ significantly on the surface. Causal contrasts appear in many guises, some more obvious than others. They also appear in many scientific contexts, from the experimental to the observational to the purely theoretical.

Causal contrast diagrams are philosophically significant. They are a window into one of the key practices of scientific epistemology: causal inference. I suggest that this goes far in explaining why scientists, when reading a paper, turn to the diagrams first. A study’s key results can often be found there. Intriguingly, diagrams are often much more than merely a preferred representational tool for causal inferences. Diagrams themselves often constitute evidence: think of the ubiquitous photographs of electrophoresis gels in molecular biology, or the fluorescence micrograph shown above.

I call the paper “Spot the difference: Causal contrasts in scientific diagrams”. A preprint is available on the PhilSci archive, and the finished paper is about to come out in Studies in History and Philosophy of Biological and Biomedical Sciences.