II. KEY EPIDEMIOLOGICAL CONCEPTS

Two epidemiological measures are particularly important in this context, and although they are related, they must be distinguished. They are relative risk (RR) and attributable fraction (AF, also known as attributable risk). RR is a measure of how much more common a given condition is among people who are subject to a given exposure than among those who are not.Footnote ⁴ It is calculated as follows:

A couple of points about RR must be emphasized. First, it is crucial to realize that “risk” in this context means nothing more than incidence over a specified time interval.Footnote ⁵ It does not denote the product of the probability that a harm will occur and the gravity of that harm; in fact it does not even denote a probability, strictly speaking, without ancillary assumptions about the nature of probability. It is a purely statistical measure of the relative frequency with which a disease occurs in exposed and unexposed populations.

Second, although RR can be used to measure effect size, the mere performance of the above calculation has no intrinsic significance for causal inference; this calculation does not by itself amount to a causal inference. This follows from the previous point that “risk” in this usage denotes a purely statistical measure.Footnote ⁶ Thus before a figure for RR can be (reasonably) appealed to in support of specific causation, it must be backed by a sound causal inference at the general level. Courts often need to assess general-level inferences of this kind.Footnote ⁷ In particular it must be established that the RR is not due to anything other than the exposure—that there are no uncontrolled confounders and no artifacts arising from the manner in which subjects were selected and classified as exposed or diseased.Footnote ⁸ Even if there are independent grounds for supposing there is some causal link between exposure and harm, accounting for these potential sources of a false causal inference is necessary for the RR to be rationally understood as saying anything about that link.

The principles governing general causal inference are not the topic of this paper.Footnote ⁹ So henceforth it is assumed that all the RRs we discuss are backed by sound causal inferences and in particular that the possibility of confounding, misclassification, and other problems have been adequately addressed, so that the court accepts that the difference that the RR expresses between risk among exposed and unexposed is explained—caused—solely by the exposure.Footnote ¹⁰

An example: suppose (roughly correctly) that 15 percent of British male smokers get lung cancer, whereas 1.5 percent of British male nonsmokers do. Then RR = 15% / 1.5% = 10. This tells us that lung cancer is ten times as common among British male smokers than British male nonsmokers. If this RR is used to prove specific causation, it must first be accepted that the causal explanation for this difference is smoking.

The other epidemiological concept that is important in this context is AF. This is the proportion of a disease burden within a population that is “attributable” to a given exposure. Before we address the scare quotes, let us set out the calculation:

So in our smoking example, the fraction of lung cancer attributable to smoking would be (15% − 1.5%) / 15% = 0.9, or 90%, which is to say that that 90 percent of cases of lung cancer among smokers are “attributable” to smoking.

The word “attributable” is not transparent. First, AF (like RR) is a statistical measure only; it can be used to express information about a causal link, but the mere possibility of performing the calculation is no proof of causation, and merely performing the calculation is no replacement for a causal inference.

Second, even where a causal inference to explain the AF is warranted, the word “attributable” is potentially misleading, as Greenland and others point out. These authors advocate a distinction between excess and etiological fraction.Footnote ¹¹ AF as I am describing it is excess fraction, in the sense that it tells us how many excess cases there are among the exposed group (as a fraction of the total number of cases in that group). Granted a sound causal inference, we can infer that all the excess cases are caused by the exposure. But we cannot infer that the remaining cases are not caused by the exposure. The etiologic fraction—the cases in which the exposure makes a causal contribution—could be larger. Roughly speaking, this is because, in the absence of substantive biological assumptions, it is possible that the exposure could contribute to cases that would have occurredFootnote ¹² even without the exposure.Footnote ¹³ For example, it might be that smoking is a cause of lung cancer even among some of those who would have developed it anyway. The fact that a person would have developed lung cancer anyway does not offer automatic protection against the carcinogenic effects of cigarette smoke (a point we return to in Section IV). We cannot assume, without supporting biological evidence, that when an exposure is among the causes of a case of a disease, background factors are thereby excluded from also being causes of that case.Footnote ¹⁴ Thus when I use AF, I mean excess fraction; there is no way to calculate etiologic fraction from empirical data without supplementary assumptions.Footnote ¹⁵

The considerations of the preceding paragraph are so widely ignored in the judicial treatment of epidemiological evidence that I do not think I have seen them discussed judicially at all. Yet, as I argue below, they are central to the correct usage of epidemiological evidence in proving specific causation because they give rise to an epistemic asymmetry between proof and disproof that, as far as I am aware, is also without clear and explicit judicial recognition.Footnote ¹⁶

Before moving to discuss the uses that are made of these measures, it is important to appreciate that both RR and AF are specific to populations. This is obvious for AF, because a fraction must be a fraction of something, and a diseased population is the obvious candidate. But it is easy to slip into thinking of RR as a property of an exposure-disease pair without specifying the exposed and unexposed populations that the RR compares.Footnote ¹⁷ In fact, RR (like AF) is a function of exposure, disease, and population. To see why, recall that I do not specify an age range for the (fictitious) RR associated with smoking among British males. Suppose we select an age range of fourteen to eighteen. If RR was close to 1 in that group, that would not show that smoking does not cause lung cancer. The likeliest explanation would be that few teenagers get lung cancer regardless of whether they smoke.Footnote ¹⁸ It follows that there is no such thing as the RR of lung cancer for smoking, independent of the specification of an exposed populationFootnote ¹⁹ and an unexposed population that is suitable to act as a control.Footnote ²⁰

Finally, it is evident that RR and AF are related, as they can be calculated from the same data. The formula for calculating AF from RR (as they are defined here) is:Footnote ²¹

This calculation is significant for our purposes because it has sometimes been used in legal contexts to calculate the probability of specific causation from epidemiological data, that probability being equated to AF.Footnote ²² For example, some courts would use our cigarette data to calculate a probability that a particular British male smoker's lung cancer was caused by smoking at 0.9. Coupled with an assumption to the effect that the appropriate standard of proof can be represented by a probability of > 0.5, this would yield the consequence that specific causation was proved; whereas RR of 2 or less would yield a probability of 0.5 or less, meaning causation was not proved. The equation of AF with probability of causation, as defined here, has been heavily criticized, and rightly so, by epidemiologists such as Greenland. We consider these criticisms in Section IV. The auxiliary assumption concerning the standard of proof and, more generally, the relevance of this kind of evidence for proving specific causation are also heavily criticized, this time by legal scholars. We consider some of these criticisms in Sections V and VI. But first let us consider some of the ways that courts in England, Scotland, and the United States have handled attempts to prove specific causation using epidemiological evidence.

III. LEGAL ATTITUDES TO EPIDEMIOLOGICAL EVIDENCE

It is possible to distil three main attitudes toward the use of epidemiological evidence in proof of specific causation out of the rather convoluted jurisprudence and commentary on the topic:

• • that epidemiological evidence is irrelevant to proof of specific causation;

• • that where only epidemiological evidence is available, normal causation rules may sometimes be relaxed, so increase in risk can satisfy the causation element; and

• • that the threshold for proof of specific causation using epidemiological evidence is RR > 2.

These attitudes are not mutually exclusive. The increased-risk approach might be motivated partly by the view that epidemiological evidence is strictly irrelevant; and the view that RR > 2 is the threshold for proof is also compatible with allowing proof of increased risk where RR ≤ 2 but policy considerations suggest that the claimant should succeed. Let us examine each in turn.

IV. THE SIGNIFICANCE OF RR > 2

The Reference Manual on Scientific Evidence attempts to explain the significance of RR > 2 as follows:

The Manual goes on to put the same test in terms of AF > 50%: “When the attributable risk exceeds 50% (equivalent to a relative risk greater than 2.0), this logically might lead one to believe that the agent was more likely than not the cause of the plaintiff's disease.”Footnote ⁷²

This reasoning equates the probability of causation (PC) with AF, which in turn is related to RR, as shown in Section II, implying that:

According to this formula, sometimes known as the probability of causation (PC) formula, when RR = 1, PC = 0; and when RR reaches 2, PC will reach 50 percent.Footnote ⁷³

There are two problems with the reasoning cited in the Reference Manual. First, it is unclearly stated. Second, it is fallacious.

Regarding clarity, even if we accept the premise that RR = 1 means no effect (strictly speaking a false premise, as we shall see), we are given no reason for thinking that when RR reaches 2, there is a 50 percent probability that the exposure caused the disease. The word “Thus” at the start of the third sentence cited in that passage does not constitute a reason. Similarly, we are given no reason for thinking that AF = 50% implies a probability of causation of 50 percent (and the word “logically” does not amount to a reason). These are non sequiturs. The same lack of clarity infects most statements both judicial and extrajudicial.Footnote ⁷⁴

Presumably, the reasoning is that when AF = 50%, and a general causal inference has been accepted, then 50 percent of the cases in the exposed population are caused by the exposure. And therefore the chance that the exposure is a cause of a case of the disease randomly selected from the exposed population of sufferers exceeds 50 percent when AF exceeds 50 percent (and RR > 2). The remaining assumption is that claimants are randomly selected with respect to the epidemiological evidence.

But the reasoning just cited is fallacious, exemplifying a common error. The error is evident from the discussion in Section II. As pointed out there, AF as it is being used in these passages is a statistical measure referring to excess fraction—the excess cases (as a proportion of the total cases in the exposed group) that occur in the exposed group, as compared to the unexposed. It is possible for the etiologic fraction—the fraction of cases caused by the exposure—to be larger, perhaps much larger.Footnote ⁷⁵ Therefore it does not follow from an AF of 50 percent that 50 percent of the cases in the exposed group are caused by the exposure, even assuming—as we are—that the exposure causally explains the AF and thus that the general causation issue has been settled.

Moreover, the formula relating AF and RR (AF = 1 − 1/RR) holds only when AF is understood as an excess, not etiologic, fraction. Therefore, contrary to what is asserted in the passage cited from the Manual, RR = 1 (or AF = 50%) does not mean that the agent is not causing the disease in the population in question. It implies only that the agent has no net effect on the incidence of the disease—no net effect on the number of new cases in the time period that these figures concern. RR = 1 means no net effect, but no net effect does not mean no effect. By the same token, RR = 2 does not imply a 50 percent likelihood of individual causation. It implies only that the exposure gives rise to a net excess in the proportion of cases in the exposed population compared to the unexposed population that is equal to 50 percent of the total cases in the exposed population.Footnote ⁷⁶

This might look like a purely theoretical objection. But it is not. The PC formula relies on substantive biological assumptions that are often violated.Footnote ⁷⁷ Most obviously, it assumes that the exposure is not a cause of the disease among that proportion of cases that you would expect to find in an unexposed population. This is flagrantly ridiculous in many cases. Consider, for example, a fictitious group of Himalayan porters. One might imagine that carrying heavy loads up and down mountains increases their risk of back injury. Among those porters suffering back injury will be some who for anatomical reasons would have developed a back injury anyway. But having a weak back does not protect these porters from the effects of carrying heavy loads. On the contrary, it is quite possible that carrying a heavy load will be a cause of back injury among many or even all those porters whose backs were such that they would have developed a back injury even in a less physically demanding profession. Endorsing the PC formula amounts to endorsing the astonishing view that a person who would develop a disease without the exposure in question is thereby protected from the effects of that exposure: that having a weak back will protect a Himalayan porter from the harm that carrying a heavy load would otherwise do to his back. It does not take any great conceptual sophistication to see that this is an error.

In a series of articles, Greenland provides a number of examples of ways that the PC formula can underestimate the probability of causation. An exposure might accelerate a disease so that those who are at risk die before featuring in the study.Footnote ⁷⁸ An exposure might cause the disease in some and prevent it in others, which will not show up in RR or AF, as these are measures of net impact.Footnote ⁷⁹ In short, when epidemiological studies indicate that RR > 1 and that this is to be explained causally, that does not settle the question as to what proportion of the exposed cases is due to the exposure.

There is, however, an asymmetry here. Although RR and AF can massively underestimate the probability of specific causation, they cannot overestimate it, assuming—as we are—that the general causation issue has been settled (and that our inquiry is prior to, feeds into, and does not replace a weighing of all the relevant evidence). This is because to settle the general causation issue, it is necessary to infer that the difference between the exposed and unexposed groups is not due to some defect in the comparison (e.g., uncontrolled confounders; misclassification of subjects as exposed or diseased)Footnote ⁸⁰ but is in fact caused by the exposure. Granted this inference, it follows that all the excess incidence must be caused by the exposure. That is just what it means to accept that potential defects in the comparison have been eliminated and the general causal inference is sound. For example, it would simply not be accurate to claim that AF for lung cancer among British male smokers compared to nonsmokers is 90 percent, nor that RR is 10, if there were some other live possibility as to why smokers develop lung cancer so much more often.

Thus Greenland and James Robins write, “Epidemiologic data does place a nonzero lower bound on the probability of causation when [AF] > 0.”Footnote ⁸¹

Because excess fraction and etiologic fraction may not be equal (the latter being larger under many if not most biological models),Footnote ⁸² it is fallacious to equate the probability of causation in a randomly selected specific case with AF (and thus with 1 − 1/RR). However, although the etiological fraction may be larger than the excess fraction, it cannot be smaller—consistent with the assumption that the general causation issue has been settled with respect to the AF figure in question. Accepting that an exposure causes a certain excess proportion of cases in the exposed group logically entails that at least that proportion of cases features the exposure as a cause. But as shown above, it does not logically prevent there being more cases caused by the exposure. To cite an AF of 90 percent or an RR of 10 for male British smokers with lung cancer would be inaccurate, or at least highly misleading, if there remained some live possibility of an alternative explanation for at least some of the excess incidence, whereas these figures remain accurate even if it is suspected (as it may reasonably be) that smoking plays a role in more than 90 percent of cases of smokers with lung cancer. AF and RR express numerical differences between incidences in populations, and explaining those differences is not equivalent to explaining the incidence in either population.Footnote ⁸³

This suggests that the PC formula should be replaced with a “PC inequality”:

Or, equivalently:

These inequalities require two caveats. First, they assume that the incidence in the exposed group is greater than that in the unexposed group, that is, that RR > 1.Footnote ⁸⁴ This is a plausible assumption in the context of litigation, because if the harm is more common among the unexposed group, this suggests prima facie that the exposure has a net protective effect, and it is hard to see how a net protective effect would generate claims for damages in the way that in fact net harmful effects have done. In any case it is easy to check whether the assumption is satisfied. Second, as emphasized at the outset, the formula must not be treated as determinative. Other evidence may bear on the probability that the fact finder ought to assign to causation; to this extent the aforementioned Manual is quite correct. Epidemiological evidence must be weighed against other relevant evidence.

The epistemic position with regard to epidemiological evidence is thus surprisingly simple, though delicate to state clearly. Epidemiological evidence says not how probable specific causation is but how improbable it is not.Footnote ⁸⁵ Once the general causation issue is settled and a figure for RR or AF is accepted, it follows that at least the proportion of cases indicated by the AF is caused by the exposure. If we accept that the claimant is a randomly selected exposed person, then the force of that evidence is that the probability that the exposure caused the harm in that case is not less than AF.

However, this proposal does not answer Wright's objection that epidemiological evidence is irrelevant to ex post probabilities altogether. So far I am ignoring that objection for the sake of clear statement. Before we turn to this conceptual objection to epidemiological evidence, it is worth noting that the foregoing reasoning applies equally to the but-for test. Suppose that as well as excess and etiologic fraction, we define but-for fraction: the proportion of an exposed population who would not have developed the disease but for the exposure. The but-for fraction could be much greater than the excess fraction (because the exposure could prevent the disease in some while causing it in others, etc.). But it could not be less—provided that a causal explanation of the excess fraction is accepted. That would tantamount to claiming that the excess fraction arose due to some interfering factor or factors and not because of the exposure, or else that it was not caused at all, which is even more strange. On this basis it is a paradigmatic inference that but for the exposure, the excess would not have occurred—for any viable interpretation of “but for.”Footnote ⁸⁶

Jonathan Schaffer has put it to me (in correspondence) that the asymmetry I seek to capture with my “PC inequality” arises because of an asymmetry in my starting assumptions. My conclusion follows if we make the epistemic assumption that a causal inference is warranted at the general level but refuse to make the biological assumptions necessary to move from my PC inequality to the PC formula I reject. But why make the epistemic assumption and not the biological one?

My answer is, first, that it is realistic to assume that epidemiological evidence sometimes warrants a general causal inference, and so it is reasonable and, I hope, useful to confine the discussion to what follows from that. It is not, however, realistic to assume a given biological model for diseases in this context, because we are focusing on the situation where the biology of the disease is not well understood. As we see at the outset, this is typically the reason for appealing to epidemiological evidence in the first place. Moreover, the biological facts that must obtain for epidemiological evidence to provide an upper bound on the probability of causation are rarely instantiated. Greenland and Robins write, “We know of no cancer or other important chronic disease for which current biomedical knowledge allows one to exclude mechanisms that violate the assumptions needed to claim that PC = [AF].”Footnote ⁸⁷

More generally, as my Himalayan porter with the bad back is supposed to illustrate, it is quite implausible that the requisite assumptions are widely instantiated. Interaction is common, and exposures that simultaneously protect against the effect of other exposures when they cause a disease are rare.

My second reply to Schaffer's point is that if we want to find out what the epidemiological evidence says about specific causation, we must make the assumption that it is good. Bad epidemiological evidence, like bad evidence more generally, does not say much about anything (or, at least, what it says cannot be stated in a general way). However, we do not need to make a biological assumption about the nature of the disease in question merely in order to understand what epidemiological evidence says, especially not when these assumptions are so rarely satisfied. Granted, the epidemiological evidence might say something different in the light of further knowledge about the biology of the disease; but this, again, departs from the question I want to tackle, which is what the epidemiological evidence itself says, before other evidence is considered.

V. THE EPISTEMIC SIGNIFICANCE OF EPIDEMIOLOGICAL EVIDENCE

If epidemiological evidence says anything about specific causation, then what it says is in the form of an inequality: in the absence of other evidence, the probability that the exposure caused the harm in a randomly selected case is at least the attributable fraction (AF). But there is a strong current of opinion among both judges and commentators that epidemiological evidence is not relevant to the proof of specific causation in this direct way: that it does not, in fact, say anything about how probable it is that the exposure caused the harm in a particular case.

There are in fact a number of different objections on this theme. Let us distinguish epistemological from legal objections, where the latter claim something more than just that epidemiological evidence is epistemically deficient with regard to the specific causation issue. We consider legal objections in the next section.

The epistemological objections turn on the fact that epidemiological evidence concerns populations and not individuals. But as argued in Section III, this bare fact does not amount to a cogent objection to the epistemic relevance of epidemiological evidence to individuals, and in fact both conceptual and empirical arguments demonstrate that epidemiological evidence is relevant to individuals in some circumstances.

One possible way to flesh out the objection is to argue that coherent use of epidemiological evidence requires knowing something about the mechanism(s) by which the exposure causes the harm.Footnote ⁸⁸ A disambiguation is necessary here. On one understanding, what we need to know is a general scientific fact about how the exposure causes the harm when it does so. As Jane Stapleton emphasizes, this will not get us any further with our question; to prove specific causation, we need to know how the harm in fact was caused on this particular occasion.Footnote ⁸⁹ Thus the other disambiguation of the objection is that we must know what mechanism gave rise to this particular case of disease before we can use epidemiological evidence. But if we know that, then we have settled the specific causation issue already, and the epidemiological evidence is entirely redundant. The requirement that we know which mechanism operated on this particular occasion thus cannot be a precondition on the relevance of epidemiological evidence; rather, it is a denial of its relevance. The implication of the denial is that we must always know what mechanism gives rise to an effect in order ever to know that causation occurs. But this is radically implausible. I can know that drinking whisky caused my hangover without having the faintest idea how. Moreover, to insist that I must always know the mechanism underlying a causal phenomenon is to plunge into a regress, because the mechanisms in question will typically also involve causal relations (at least in the sorts of cases we are concerned with here).Footnote ⁹⁰ Thus the objection fails on either disambiguation.

A different line of argument is developed by Wright, who distinguishes ex ante and ex post probabilities. According to Wright, the epistemic worry is that statistical information derived from population-level studies “takes the eye off the ball by asking what was likely to happen ex ante, or what the abstract statistical odds were, rather than focusing on what actually happened ex post.”Footnote ⁹¹ Wright's ex ante/ex post distinction is tied up with his view of causation, which he sees in terms of causal generalizations and causal laws. A causal generalization might be that smoking causes lung cancer. A causal law would be the full specification of all those factors that are present when smoking causes lung cancer. According to Wright, we use causal generalizations because we generally have “imperfect knowledge” and therefore often cannot state causal laws.Footnote ⁹²

In this context, an ex ante “causal probability” is the probability that “the causal law underlying a causal generalization will be fully instantiated if the generalization is fully instantiated.” Footnote ⁹³ So it is the probability that the exceptionless causal law underlying “Smoking causes lung cancer” will be instantiated if a person smokes and develops lung cancer—meaning the probability that when smoking and lung cancer both occur, smoking causes the lung cancer.Footnote ⁹⁴ On the other hand, an ex post probability is “a case-specific probability, based solely on the particularistic evidence specific to a particular occasion, that the causal law underlying a possibly applicable causal generalization was fully instantiated on the particular occasion.”Footnote ⁹⁵

It is evident from these definitions that the weight of the ex ante/ex post distinction must be borne by the definition of “particularistic evidence.” Otherwise the only other distinction is whether the probability concerns the future instantiation of a causal law or its past instantiation. That distinction is surely not relevant in this context. Usually evidence as to the occurrence of an event retains its force regardless of whether the event has occurred at the time the evidence is assessed. Of course, it may be silly to rely after an event solely on evidence that was available before it happened. Predictions as to who will win a football match are disregarded after the match is played, but not because they lose their force—rather, because better evidence is available. Likewise, the problem with epidemiological evidence cannot be merely that the event in question now lies in the past. The evidence is as good for retrodiction or “postdiction” as for prediction, and Wright acknowledges this point.Footnote ⁹⁶

The distinction between ex ante and ex post probabilities, then, is not between probability of a future event and probability of a past event. Within the materials provided by the definitions offered, the distinction must therefore have to do with the kind of evidence that supports each respective kind of probability. Wright writes, “An item of ‘particularistic evidence’ is a concrete feature of a particular occasion that instantiates or negates the instantiation of one of the abstract elements in a possibly applicable causal generalization.”

In support of his distinction Wright cites Day v. Boston,Footnote ⁹⁷ where the court pointed out that the slightest evidence that a roll of a die resulted in a 6 would outweigh “all the probability otherwise.”Footnote ⁹⁸ Wright proceeds to claim that, “To prove that a causal generalization and its underlying causal law have been instantiated, one must prove that all the abstract elements in the causal generalization and the underlying causal law have been instantiated. Only particularistic evidence can establish such instantiation.”Footnote ⁹⁹

Since only particularistic evidence can bear on whether a causal generalization was in fact instantiated, and only ex post—not ex ante—probabilities are backed by particularistic evidence, only ex post probabilities can bear on whether a causal law was instantiated. Thus only ex post probabilities bear on whether a particular claimant's harm was caused by a particular exposure.

Despite Wright's strenuous efforts, the ex post/ex ante distinction remains elusive. There are several difficulties. First, all the weight is on “particularistic evidence.” But what makes evidence “particular” or “specific” to a given case? Jones has smoked twenty cigarettes a day for the last forty years. Jones, the cigarettes, the days, and the years were all particular and concrete. It is also true that he has lung cancer. The lung cancer is not abstract; it is particular and concrete. To that extent these are pieces of “particularistic evidence”; they are facts about Jones. Yet they clearly bear on the probability, which Wright wants to dismiss as ex ante, that is yielded by considering the epidemiological evidence that RR for British male smokers, of which Jones is one, is 10.

One possible response is that the facts cited are not particular, because they do not mention anything special about Jones's smoking or lung cancer. They go equally for many other smokers. But that will always be true unless we provide unique features of Jones's situation. Yet this is not a sound requirement on evidence. First, why should a claimant prove that her case is unique in order to succeed? It is possible that two cases may be alike, if not tout court, at least on the legally salient facts before the court. Why should a case turn on the extrinsic fact that other, similar cases exist? Two throws of a die may both result in a 6. Moreover it is the similarities with other occasions on which a die has come up 6 that allows an eyewitness to confirm that this was what happened on a particular occasion and indeed to express what she saw to an audience.Footnote ¹⁰⁰ Second, in legal practice cases are usually considered to be easier to settle when they share features with other cases. Third, it is a fundamental philosophical point that causation is something we learn about from experience. A causal finding about an entirely alien sequence of events would be a mere guess.Footnote ¹⁰¹ To this extent there is a serious prospect that unique features of Jones's case, far from being crucial, would be epistemically irrelevant, because it is the similarities, and not the differences, between Jones's case and others that take center stage in any causal inferences we might make.

It cannot be, then, that particularistic evidence consists in features of a situation that are unique. Such features may be wholly irrelevant to the inference at hand; and nonunique features might be germane.

There is a more basic and perhaps obvious problem with Wright's proposal, however: it rests on a piece of speculative metaphysics. The view of the nature of causation and its relation to laws that Wright espouses is contested by many philosophers. For Wright, a causal law is an exceptionless regularity, and causation occurs when the regularity is instantiated. There are many philosophical objections to the claim that laws of nature are exceptionless regularities. They are serious objections, and in consequence, the popularity of regularity theories of law and causation among philosophers has been in decline since the second half of the last century. None of this means that they are indefensible or that Wright is wrong about the nature of causation. But as others have noted,Footnote ¹⁰² Wright does not acknowledge the full force of the difficulties that his view faces nor the strangeness of basing a practical recommendation on an uncertain metaphysical theory. It is wrong, epistemically and morally, to justify excluding epidemiological evidence at law on the basis of a controversial stance in speculative metaphysics. The basis of Wright's argument is far too uncertain and contested to form the basis of any legal doctrine. Even philosophers who agree that laws of nature are exceptionless regularities would probably hesitate to deploy their theory in this way. If Wright's position is to be supported, another, less speculative basis must be found.

A better interpretation (which Wright would not accept) might be that evidence is particularistic when it is sensitive to the truth of the hypothesis in question. On this interpretation, particularistic evidence as regards the claim that Jones's smoking caused his lung cancer does not consist in unique features of Jones's situation. He is demanding features of the situation which would be different if Jones's smoking was not caused by lung cancer.Footnote ¹⁰³ Thus it might be objected that statistical evidence of the sort provided by epidemiology is not sensitive to the correctness of the inference in any particular case. The evidence would be just the same if Jones's lung cancer were not caused by smoking as if it were. Particularistic evidence, on the other hand, might be understood as evidence that would have been different if the hypothesis it is adduced to prove were false. This interpretation is an expression of the epistemological stance known as counterfactual reliabilism, according to which a good inductive inference must be such that the evidence is sensitive to the truth-value of the conclusion reached.Footnote ¹⁰⁴ Statistical evidence clearly violates this condition in application to individuals, because ex hypothesi the evidence is the same for every individual and therefore warrants the same conclusion for each.

This objection raises difficult questions. Although some philosophers endorse sensitivity conditions on evidence, others roundly reject them.Footnote ¹⁰⁵ Again, we should be wary of settling practical disputes by resorting to philosophical views that are themselves actively disputed. Moreover, even if this understanding of particularistic evidence does distinguish it neatly from epidemiological evidence, it hardly follows that the latter must be ignored. On the contrary, if it can be shown that ignoring epidemiological evidence is a bad idea, that would be a problem for counterfactual reliabilism.

And indeed, the second serious problem with the proposed distinction between ex ante and ex post probabilities is that ignoring the latter commits an epistemic fallacy and demonstrably leads to errors. Contrary to what might seem intuitive, it is always necessary to weigh what Wright would label the ex ante probability against whatever sorts of evidence Wright would accept as particularistic. In a nutshell, this is because you cannot simply disregard old evidence when new evidence comes in.

For example, suppose that we have an ex ante probability of 1/6 that a die will come up 6. Suppose we throw the die and it comes up 6. In normal circumstances, we are not aware of weighing up a 1/6 statistical probability against the (unquantified) probability that our eyes are functioning correctly. Indeed, we are probably not aware of it because we probably do not do it. But now suppose that instead of turning up a 6, the die turns into a butterfly. Then it would be both reasonable and intuitive (if we keep our wits about us) to compare the ex ante probability (albeit not readily quantifiable) of this occurrence with the ex post probability based on the particularistic evidence provided by our visual experience. The latter is 1, because that is what we see; but it is surely reasonable to doubt that the die really turned into a butterfly. Because the particularistic evidence in both the 6 case and the butterfly case is the same, the ex post probability to which it gives rise is presumably the same. Yet it is surely rational to be less certain that the die really did turn into a butterfly than that you really did roll a 6 in the first case. That is because it is surely rational to take into account the background frequency with which events occur in the relevant circumstances when deciding whether a particular event did in fact occur.Footnote ¹⁰⁶ To deny this is to make an epistemic error.

There is a plausible explanation for the prevalence of the error of ignoring epidemiological evidence in proof of specific causation. The error is an instance of the well-documented human tendency to ignore “base rates” in calculating probabilities.Footnote ¹⁰⁷ A base rate is, roughly, the frequency with which a given event generally occurs in the circumstances in question. If this is not taken into consideration when estimating the probability that an event has in fact occurred, then errors result. To take a well-known example, if a disease occurs among one in a thousand people in a population, and a medical test for the disease has a 5 percent false-positive rate,Footnote ¹⁰⁸ it would be erroneous to conclude that an individual testing positive has a 95 percent chance of having the disease. On average, for every thousand people tested, fifty will test positive when they do not in fact have the disease. In addition, assuming no false negatives, on average a further one person on average will test positive because he or she has the disease. The correct probability that a given positive test result in this population indicates the disease is therefore one in fifty-one, or roughly 2 percent. And that means that the probability that the positive test result is caused by the disease in any individual case is about 2 percent. In this case, ignoring the epidemiological evidence as to the prevalence of the disease in estimating the probability of specific causation leads to a huge error—an estimate of 95 percent when the correct figure is about 2 percent.Footnote ¹⁰⁹

The relevance of this example is that epidemiological evidence is typically problematic in cases where there is no test to distinguish those cases of the disease that are caused by the exposure from those that are not. Were a test available to distinguish, say, cancers caused by smoking from those that are not, presumably that would amount to particularistic evidence.Footnote ¹¹⁰ Yet this evidence would not entirely displace epidemiological evidence—or at least, it should not, epistemically speaking. Rather, it ought to be weighed against that evidence. But this seems incompatible with a strong distinction between ex ante and ex post probabilities, where the latter are supported by particularistic evidence and the former derive from epidemiological evidence. To this extent, the mooted distinction between ex ante and ex post probabilities represents an epistemic fallacy.

It might be replied that both the false-positive rate and the base rate are ex ante probabilities. In the medical test example, the false-positive rate is presumably drawn from statistical data just as much as is the base rate of the disease. But even granting that assumption, the objection is a weak one. For it leaves the objector committed to ignoring not only base rates but even false-positive rates. This is a reductio ad absurdum of the suggestion that ex ante probabilities are irrelevant to determining whether particular events have occurred. For it is obviously absurd to ignore the reliability statistics for a medical test when forming a view as to the probability that the disease-event it purports to detect has occurred.

Wright illustrates some of the problems he perceives in the use of statistical evidence with a discussion of Hotson v. East Berkshire Area Health Authority.Footnote ¹¹¹ There it was found that there was a 75 percent chance that a permanent injury suffered following a delay in medical treatment would have occurred anyway and therefore that the burden of proof of causation was not discharged. Wright argues that this is a non sequitur.Footnote ¹¹² I agree, but the criticism here has nothing to do with the use of statistical evidence per se. It is a criticism of the use of the but-for test. The kernel of Wright's argument is that even if the permanent injury would have occurred without the delay in treatment, it does not follow—and indeed seems unlikely—that the delay was not among the causes of the permanent injury. It seems to me that this criticism is correct. It concerns the misunderstanding of epidemiological evidence identified in Section IV of this paper and it is answered by the proposal made there that epidemiological evidence should be regarded not as providing a figure for the probability of causation but as assisting in the estimation of a lower bound.

Let us finish this section with two slightly different objections. The first is that “probability” remains undefined. This is not the place for a discourse on interpretations of probability.Footnote ¹¹³ The epidemiological measures AF and RR lend themselves to a frequency interpretation, if they are to be interpreted as probabilities at all. A frequency interpretation sees a probability as the frequency of an event in the indefinitely long run (e.g., the proportion of heads you would get if you endlessly tossed coins). Epidemiological evidence arguably provides a good estimate of this sort of probability. The probability for specific causation might be understood as a single-case chance conditional on the evidence, what Hugh Mellor calls an epistemic probability;Footnote ¹¹⁴ or it might be a rationally constrained subjective degree of belief, sometimes called a credence. In either case, we would need some principle along the lines of David Lewis's well-known Principal Principle, Footnote ¹¹⁵ which states roughly that credences ought to be apportioned to objective chances where the latter are long-run frequencies. (If epistemic probabilities are preferred to credences, then we would need some similar principle relating the single-case chance, given evidence regarding a long-run frequency) The Principal Principle is a subject of philosophical dispute, but some version of it is highly plausible—to the extent that it is regarded by some as a necessary condition on any adequate theory of objective chance.Footnote ¹¹⁶ As far as I can see, nothing further of relevance in this context turns upon the interpretation of probability that is chosen. All that is required is that it makes sense to think of an event as having a degree of probability in the light of given evidence, and that that probability can change in the light of further evidence.Footnote ¹¹⁷

Second, it might be objected that this line on epidemiological evidence commits us to an implausible stance on the notorious “blue bus problem,”Footnote ¹¹⁸ which is intended to illustrate both the attractiveness and the silliness of allowing proof by purely statistical evidence.Footnote ¹¹⁹ Suppose a claimant is hit by a bus she does not see, but it is known that 75 percent of the buses in town are run by the Blue Bus Company. Does that mean that there is a 75 percent probability that she was hit by a blue bus, and moreover, should she succeed on that basis? My approach to epidemiological evidence might appear to support a positive answer, at least to the first part of the question (we deal with legal standards of proof in Section VI).This is at least in tension with a body of judicial and academic opinion.

But the objection is not accurate. The blue bus problem concerns the use of statistics more generally, including what Wright calls “naked statistics”Footnote ¹²⁰ that are not supported by any causal inference. We, however, are concerned with statistical measures that are causally explained. It might be that the remaining 25 percent of buses are run by freelance cowboys who account for almost all traffic accidents in the city. A closer analogy would be a case where 75 percent of injuries relevantly like the claimant's are caused by Blue Buses. In that case, the significance of that evidence would indeed be a 75 percent chance that the injury was caused by a Blue Bus.Footnote ¹²¹ But in that case, we would not be using naked statistics as the basis for inferring specific causation. We would first be clothing the statistics in a general causal inference; and it is the general causal claim, quantified but not exhausted by the statistical fact, that licences the inference to the specific causal claim.

It does not follow, in any case, that the claimant must succeed against the Blue Bus Company. Indeed, the question, properly put, is not whether she must but whether she can succeed.Footnote ¹²² There may be other evidence (as I repeatedly emphasize in the epidemiological case). Moreover, the lack of other evidence in a case like this may itself tell heavily against the claimant, given that it is relatively easy to identify the color of a bus. Then the difference between this case and the epidemiological one concerns not what the evidence says but how clear the total evidential picture is, and the clarity of that picture depends in part on what evidence might in principle be available.

Of course, the blue bus problem may be set up so as to make the lack of other evidence insignificant: the bus hit from behind, it was misty, and so on.Footnote ¹²³ Such attempts deserve some suspicion: common sense is not easily instructed to ignore the fact that when buses strike, there is usually more than just statistical evidence available. This is because buses are big, noisy, and full of people. However, diseases are not like buses. When trying to prove specific causation using epidemiological evidence, there is no possibility of eyewitness testimony. When only epidemiological evidence is used, that is generally because clinical science cannot produce anything better. If a claimant sought to rely on epidemiological evidence to prove causation for a harm that was comfortably within the scope of clinical science, they would be on shakier epistemic ground, because the total evidential picture, taking into account the evidence that might in principle have been available to the claimant, would be weaker.Footnote ¹²⁴

What does, however, remain to be discussed is the legal significance of the probabilities that epidemiological evidence can, if my argument is right, confer upon specific causation. Let us turn to that.

VI. THE LEGAL FORCE OF EPIDEMIOLOGICAL EVIDENCE

Even if it is accepted that epidemiological evidence has epistemic force of the sort and degree I describe above, its legal force remains to be determined. In particular, it does not follow from a probability of specific causation of more than 50 percent conferred by epidemiological evidence that a claimant must succeed. The simplest reason for this is the point already rehearsed a number of times: that the probability conferred by the fact finder must depend on all the evidence and not just the epidemiological evidence. But let us set that point aside—for example, suppose that only epidemiological evidence in the form of an RR or AF backed by a good causal inference is available for the proof of specific causation (and it is not reasonable to expect any other kind of evidence, given the current state of medical science). Does epidemiological evidence satisfy the legal standard of proof, and if so, at what level of AF and RR?

It seems to me that once the epistemic relevance of epidemiological evidence has been admitted, legal grounds for excluding it would need to be very compelling indeed. Take, for example, Lord Nimmo Smith's decision to refuse compensation to Mr. McTear's widow, a decision that he would have maintained even if he had found the general causation issue proved at a level of RR = 10.Footnote ¹²⁵ On average, faced with ten such claimants, Lord Nimmo Smith would decide wrongly on this issue for nine of them. This is uncontestable; what is contested is the relevance of this fact to making a decision in any of the cases. But if the argument of Section V is correct, this fact is relevant. And Lord Nimmo Smith probably decided wrongly in Mr. McTear's case, assuming that a probability of 0.9 or greater (which, by the argument of Section IV, the evidence shows) falls within the scope of “probably.” As a matter of natural justice, it seems to me that the law must find a very good reason if it is to endorse findings of fact which, like Lord Nimmo's, are probably false on the available evidence.

One such reason is precisely that a probability of 0.9 or more, or indeed any numerical probability, does not fall within the legal meaning of “probably.” Thus Charles Nesson writes:

Stripping away the rhetoric, there are two points here. The first is the negative point that probability, in a legal context, is not a mathematical concept, which is presumably supposed to imply that it cannot or should not be quantified and thus is not properly dictated by evidence that yields mathematical probabilities (numbers between 0 and 1). The second is the positive point that probability in the legal context is not a purely epistemic notion at all but includes normative considerations motivated by justice.

The negative point has been developed by other commentators into a distinction between a quantified probability attached to an event in some putatively irrelevant way and the notion of probability employed in or required to satisfy the standard of proof. For example, Steve Gold writes, “Juries should not be instructed that the preponderance standard means that plaintiffs must prove a fact probability greater than 50%. Rather, they should be instructed that plaintiffs must establish certain facts . . . by evidence which convinces juries that the fact is more likely true than not.”Footnote ¹²⁷

More recently, a similar line is argued by Wright, who maintains that the correct standard of proof for this element of this kind of liability is preponderance of evidence and that this is not accurately represented by “a 50+ percent statistical probability,” as a matter either of logic or of psychology.Footnote ¹²⁸ Wright claims that the preponderance-of-evidence standard is satisfied by attainment of “the slightest degree of belief” in the truth of the proposition to be proved.Footnote ¹²⁹

Wright seems to be opposing the expression of a degree of belief as a number between 0 and 1 and advocating instead a different meaning for “degree of belief”—a meaning that implies that even if you have only the slightest degree of belief, you do believe that the event in question occurred. It is indeed arguable that quantifying degree of belief in this way involves some fiction. It does not follow, however, and it is not true that evidence that presents quantified probabilities should have no effect on our beliefs. Even if we accept Wright's conception of a degree of belief and of its relation to the standard of proof, it does not follow that we must accept only “unquantified” probabilities and reject “statistical” ones.

In various places Wright claims that the probabilities relevant to the degree of belief whose formation amounts to satisfaction of the standard of proof are not quantified. For example, he says:

In the previous section I dealt with the objection to ex ante probabilities. It remains to consider the potential objection that only unquantified probabilities are legally relevant. There is surely no plausibility to this objection. It is implausible that a probability should be epistemically irrelevant merely because it is quantified, as shown in the previous section. And once epistemic relevance is accepted, some positive grounds need to be found for ignoring this evidence. The mere fact that a probability is quantified does not in itself provide any such grounds.

Thus once it is accepted that quantified probabilities can inform beliefs, we face a question as to how they relate to the legal standard of proof. This interpretive issue cannot be ducked. Suppose Nesson is correct that probabilities in law are not usually quantified, and Gold and Wright are correct that the standard of proof is not best expressed as a probability in excess of 0.5. The emerging question is: When should a fact finder form “the slightest degree of belief” that the event in question occurredFootnote ¹³¹ when faced with a quantified probability that that event occurred (and no further evidence is available)? When is the preponderance-of-evidence or more-likely-than-not standard satisfied?

In the civil case, there is surely only one right answer: when the only evidence is a quantified probability whose accuracy is not in dispute, the standard of proof is met by when the numerical probability exceeds 0.5. This is the only way to give effect to the principle that she who asserts proves, while sustaining impartiality. A lower standard would favor claimants. A higher standard would favor defendants. These propositions assume, of course, an equal probability of rectitude between claimants and defendants. But that is what courts ought to assume: that is impartiality.Footnote ¹³²

(Would it not be equally impartial to award damages in proportion to the probability that has been proved?Footnote ¹³³ So, for example, if the finding is of 70 percent probability of causation, then perhaps 70 percent of a full award should be made; and if the probability is 20 percent, that should be awarded. This proposal may be impartial, but it amounts to an entirely different system of awarding damages from the one that the law in this area currently employs. It would make full compensation very difficult to attain even when it is probably deserved and small awards easy to attain even when they are probably not deserved. It would require judges to quantify their overall estimates of the probability of their conclusions, which is difficult to do even in those cases where some of the evidence is quantitative. And even if the approach were confined to the present context (i.e., epidemiological evidence), it would be unworkable because of a point I stress repeatedly: that epidemiological evidence provides an estimate not of the probability of causation but of a lower bound for that probability (see Section IV). Thus “an award proportionate to the probability of causation,” if based on epidemiological evidence, could mean anything between AF and 100 percent.)

The second, positive claim that Nesson makes is that in law, “probability” is a normative rather than—or as well as—an epistemic concept. One way to pursue this point is to consider the fact that epidemiological evidence applies equally to all claimants. Thus, if the epidemiological evidence is strong enough to support a case, every claimant will succeed; whereas if it is too weak, every claimant will fail.Footnote ¹³⁴ This has an air of paradox because the very same evidence tells us that not all claimants should succeed and that not all should fail. It also has an air of injustice: courts accepting this evidence know that they are making findings that are factually wrong in at least some cases, and, prima facie, that is not just.

It may be that normative objections could be developed on this basis. But the primary concern of this paper is with the epistemic force of epidemiological evidence. To that extent I am content to leave normative objections aside.

Nonetheless, it is worth noting that any normative objections to the use of epidemiological objections cannot arise from the mere possibility of error. Every finding of fact comes with some degree of uncertainty. What is unusual about epidemiological evidence (and perhaps statistical evidence more generally) is that the degree of uncertainty is quantified. We can say how many times, in a series of ten or one hundred or one thousand findings of fact, the court will err if it relies upon that evidence alone. The mere fact that the evidence tells us this ought not to deter us from using that evidence, because the mere fact that other kinds of evidence do not quantify their own error rates does not imply that they never lead us into error. It is highly implausible to suppose that fact finders do not or should not consider the reliability of all the various kinds of evidence that count as “particularistic.” Should the fact finder ignore the fact that one witness is a reputable accountant, another an alcoholic rock star, and a third the defendant's mother? Clearly not. And there are sometimes statistical facts about the past reliability of certain kinds of evidence. It is highly implausible that ignorance of these facts improves either the epistemic or the normative situation with regard to use of this sort of evidence. It is difficult to avoid the suspicion that at least some of the resistance to the use of epidemiological (and perhaps some other statistical) evidence arises from a reluctance to face the fact of fallibility—or more precisely, the fact that fallibility over a series of findings entails either actual error or improbable luck.Footnote ¹³⁵