The Dutch book argument in turn relies on a concept of truth. Often framed in terms of bets on a horse-race, it relies on there only being one winner, which is the case for the overwhelming majority of horse races. The Dutch book argument shows that the odds, when converted to probabilities, must sum to 1 to avoid arbitrage possibilities… If we transfer this to statistics then we have different distributions indexed by a parameter. Based on the idea of truth, only one of these can be true, just as only one horse can win, and the same Dutch book argument shows that the odds must add to 1. In other words the prior must be a probability distribution. We note that in reality none of the offered distributions will be the truth, but due to the non-callability of Bayesian bets this is not considered to be a problem. Suppose we replace the question as whether a distribution represents the truth by the question as to whether it is a good approximation. Suppose that we bet, for example, that the *N*(0, 1) distribution is an adequate approximation for the data. We quote odds for this bet, the computer programme is run, and we either win or lose. If we quote odds of 5:1 then we will probably quote the same, or very similar, odds for the *N*(10^{−6}, 1) distribution, as for the *N*(0, 1+10^{−10}) distribution and so forth. It becomes clear that these odds are not representable by a probability distribution: only one distribution can be the ‘true’ but many can be adequate approximations.

I always meant to write something about how this line of argument goes wrong, but it wasn’t a high priority. But recently Davies reiterated this argument in a comment on Professor Mayo’s blog:

You define adequacy in a precise manner, a computer programme., there [sic] are many examples in my book. The inputs are the data and the model, the output yes or no. You place your bets beforehand, run the programme and win or lose your bet. The bets are realizable. If you bet 50-50 on the *N*(0,1) being an adequate model, you will no doubt bet about 50-50 on the *N*(10^{-20},1) also being an adequate model. Your bets are not expressible by a probability measure. The sum of the odds will generally be zero or infinity. …

I tried to reply in the comment thread, but WordPress ate my attempts, so: a blog post!

I have to wonder if Professor Davies asked even one Bayesian to evaluate this argument before he published it. (*In comments, Davies replies: I have been stating the argument for about 20 years now. Many Bayesians have heard my talks but so the only response I have had was by one in Lancaster who told me he had never heard the argument before and that was it.*) Let *M* be the set of statistical models under consideration. It’s true that if I bet 50-50 on *N*(0,1) being an adequate model, I will no doubt bet very close to 50-50 on *N*(10^{-20}, 1) also being an adequate model. Does this mean that “these odds are not representable by a probability distribution”? Not at all — we just need to get the sample space right. In this setup the appropriate sample space for a probability triple is the *powerset* of *M*, because exactly one of the members of the powerset of *M* will be realized when the data become known.

For example, suppose that *M* = {*N*(0,1), *N*(10^{-20}, 1), *N*(10,1)}; then there are eight conceivable outcomes — one for each possible combination of adequacy indications — that could occur once the data become known. We can encode this sample space using the binary expansion of the numbers from 0 to 7, with each digit of the binary expansion of the integer interpreted as an indicator variable for the statistical adequacy of one of the models in *M*. Let the leftmost bit refer to *N*(0,1), the center bit refer to *N*(10^-20, 1), and the rightmost bit refer to *N*(10,1). Here’s a probability measure that serves as a counterexample to the claim that “[the 50-50] bets are not expressible by a probability measure”:

Pr(001) = Pr(110) = 0.5,

Pr(000) = Pr(100) = Pr(101) = Pr(011) = Pr(010) = Pr(111) = 0.

(This is an abuse of notation, since the Pr() function takes events, that is, sets of outcomes, and not raw outcomes.) The events Davies considers are “*N*(0,1) [is] an adequate model”, which is the set {100, 101, 110, 111}, and “*N*(10^{-20},1) [is] an adequate model”, which is the set {010, 011, 110, 111}; it is trivial to see that both these events are 50-50.

Now obviously when M is uncountably infinite it’s not so easy to write down probability measures on sigma-algebras of the powerset of M. Still, that scenario is not particularly difficult for a Bayesian to handle: if the statistical adequacy function is measurable, a prior or posterior predictive probability measure automatically induces a pushforward probability measure on any sigma-algebra of the powerset of M. In fact, this is precisely the approach taken in the (rather small) Bayesian literature on assessing statistical adequacy; see for example *A nonparametric assessment of model adequacy based on Kullback-Leibler divergence*. These sorts of papers typically treat statistical adequacy as a continuous quantity, but all it would take to turn it into a Davies-style yes-no Boolean variable would be to dichotomize the continuous quantity at some threshold.

(A digression. To me, using a Bayesian nonparametric posterior distribution to assess the adequacy of a parametric model seems a bit pointless — if you have the posterior already, of what possible use is the parametric model? Actually, there *is* one use that I can think of, but I was saving it to write a paper about… Oh what the heck. I’m told (by Andrew Gelman, who should know!) that in social science it’s notorious that every variable is correlated with every other variable, at least a little bit. I imagine that this makes Pearl-style causal inference a big pain — all of the causal graphs would end up totally connected, or close to. I think there may be a role for Bayesian causal graph adequacy assessment; the causal model adequacy function would quantify the loss incurred by ignoring some edges in the highly-connected causal graph. I think this approach could facilitate communication between causal inference experts, subject matter experts, and policymakers.)

*This post’s title was originally more tendentious and insulting. As Professor Davies has graciously suggested that his future work might include a reference to this post, I think it only polite that I change the title to something less argumentative.*

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“Error statistics refers to a standpoint regarding both (1) a general philosophy of science and the roles probability plays in inductive inference, and (2) a cluster of statistical tools, their interpretation, and their justiﬁcation.”

In Mayo’s writings I see two interrelated notions of severity corresponding to the two items listed in the quote: (1) an informal severity notion that Mayo uses when discussing philosophy of science and specific scientific investigations, and (2) Mayo’s formalization of severity at the data analysis level.

One of my besetting flaws is a tendency to take a narrow conceptual focus to the detriment of the wider context. In the case of Severity, part one, I think I ended up making claims about severity that were wrong. I was narrowly focused on severity in sense (2) — in fact, on one specific equation within (2) — but used a mish-mash of ideas and terminology drawn from all of my readings of Mayo’s work. When read through a philosophy-of-science lens, the result is a distorted and misstated version of severity in sense (1) .

As a philosopher of science, I’m a rank amateur; I’m not equipped to add anything to the conversation about severity as a philosophy of science. My topic is statistics, not philosophy, and so I want to warn readers against interpreting Severity, part one as a description of Mayo’s philosophy of science; it’s more of a wordy introduction to the formal definition of severity in sense (2).

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One of the author’s results (if I could nominate one as the most important, I’d choose this one) says that if you replace your model by another one which is in an arbitrarily close neighborhood (according to the [Prokhorov] metric discussed above), the posterior expectation could be as far away as you want. Which, if you choose the right metric, means that you replace your sampling model by another one out of which typical samples *look the same*, and which therefore can be seen as as appropriate for the situation as the original one.

Note that the result is primarily about a change in the sampling model, not the prior, although it is a bit more complex than that because if you change the sampling model, you need to adapt the prior, too, which is appropriately taken into account by the authors as far as I can see.

My own reaction was rather less impressed; I tossed off,

Conclusion: Don’t define “closeness” using the TV [that is, total variation] metric or matching a finite number of moments. Use KL divergence instead.

In response to a a request by Mayo, OSS wrote up a “plain jane” explanation which was posted on Error Statistics Philosophy a couple of weeks later. It confirmed Christian’s summary:

So the brittleness theorems state that for any Bayesian model there is a second one, nearly indistinguishable from the first, achieving any desired posterior value within the deterministic range of the quantity of interest.

That sounds pretty terrible!

—

This issue came up for discussion in the comments of an Error Statistics Philosophy post in late December.

MAYO: Larry: Do you know anything about current reactions to, status of, the results by Houman Owhadi, Clint Scovel and Tim Sullivan? Are they deemed relevant for practice? (I heard some people downplay the results as not of practical concern.)

LARRY: I am not aware of significant rebuttals.

COREY: I have a vague idea that any rebuttal will basically assert that the distance these authors use is too non-discriminating in some sense, so Bayes fails to distinguish “nice” distributions from nearby (according to the distance) “nasty” ones. My intuition is that these results won’t hold for relative entropy, but I don’t have the knowledge and training to develop this idea — you’d need someone like John Baez for that.

OWHADI (the O in OSS): Well, one should define what one means by “nice” and “nasty” (and preferably without invoking circular arguments).

Also, it would seem to me that the statement that TV and Prokhorov cannot be used (or are not relevant) in “classical” Bayes is a powerful result in itself. Indeed TV has not only been used in many parts of statistics but it has also been called the testing metric by Le Cam for a good reason: i.e. (writing n the number of samples), Le Cam’s Lemma state that

1) For any n, if TV is close enough (as a function of n) all tests are bad.

2) Given any TV distance, with enough sample data there exists a good test.

Now concerning using closeness in Kullback–Leibler (KL) divergence rather than Prokhorov or TV, observe that (as noted in our original post) closeness in KL divergence is not something you can test with discrete data, but you can test closeness in TV or Prokhorov. In other words the statement “if the true distribution and my model are close in KL then classical Bayes behaves nicely” can be understood as “if I am given this infinite amount of information then my Bayesian estimation is good” which is precisely one issue/concern raised by our paper (brittleness under “finite” information).

Note also that, the assumption of closeness in KL divergence requires the non-singularity of the data generating distribution with respect to the Bayesian model (which could be a very strong assumption if you are trying to certify the safety of a critical system and results like the Feldman–Hajek Theorem tell us that “most” pairs of measures are mutually singular in the now popular context of stochastic PDEs).

In preparing a reply to Owhadi, I discovered a comment written by Dave Higdon on Xian’s Og a few days after OSS’s “plain jane” summary went up on Error Statistics Philosophy. He described the situation in concrete terms; this clarified for me just what it is that OSS’s brittleness theorems demonstrate. (Christian Hennig saw the issue too, but I couldn’t follow what he was saying without the example Higdon gave. And OSS are perfectly aware of it too — this post represents me catching up with the more knowledgeable folks.)

Suppose we judge a system safe provided that the probability that the random variable *X* exceeds 10 is very low. We assume that *X* has a Gaussian distribution with known variance 1 and unknown mean *μ*, the prior for which is

This prior doesn’t encode a strong opinion about the prior predictive probability of the event *X* > 10 (i.e., disaster).

Next, we learn about the safety of the system by observing a realization of *X,* and it turns out that the datum *x* is smaller than 7 and the posterior predictive probability of disaster is negligible. Good news, right?

OSS say, not so fast! They ask: suppose that our model is misspecified, and the true model is “nearby” in Prokhorov or TV metric. They show that for any datum that we can observe, the set of all nearby models includes a model that predicts disaster.

What kinds of model misspecifications do the Prokhorov and TV metrics capture? Suppose that the data space has been discretized to precision 2*ϵ*, and consider the set of models in which, for each possible observable datum *x*_{0}, the probability density is

in which χ(.) is the indicator function. For any specific value of *μ*, all of the models in the above set are within a small ball centered on the Gaussian model, where “small” is measured by either the Prokhorov or TV metric. (*How* small depends on *ϵ*.) Each model embodies an implication of the form:

by taking the contrapositive, we see that this is equivalent to:

Each of these “nearby” models basically modifies the Gaussian model to enable *one specific possible datum* to be a certain indicator of disaster. Thus, no matter which datum we actually end up observing, there is a “nearby” model for which both (i) typical samples are basically indistinguishable from typical samples under our assumed Gaussian model, and yet (ii) the realized datum has caused that “nearby” model, like Chicken Little, to squawk that the sky is falling.

OSS have proved a very general version of the above phenomenon: under the (weak) conditions they assume, for any given data set that we can observe, the set of all models “near” the posterior distribution contains a model that, upon observation of the realized data, goes into (the statistical model equivalent of) spasms of pants-shitting terror.

There’s nothing special to Bayes here; in particular, all of the talk about the asymptotic testability of TV- and/or Prokhorov-distinct distributions is a red herring. The OSS procedure stymies learning about the system of interest because the model misspecification set is specifically constructed to allow any possible data set to be totally misleading under the assumed model. Seen in this light, OSS’s choice of article titles is rather tendentious, don’t you think? If tendentious titles are the order of the day, perhaps the first one could be called *As flies to wanton boys are we to th’ gods: **Why no statistical model whatsoever is “good enough” *and the second one could be called *Prokhorov and *total variation neighborhoods and paranoid psychotic breaks with reality.

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My wife says that a glance at the spine gives the impression that it reads “Badass”.

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Error statistics aims to provide a philosophical foundation for the application of frequentist statistics in science. As in any frequency-based approach, error statistics adheres to what I consider to be the fundamental tenet of frequentist learning: *any particular data-based inference is deemed well-warranted only to the extent that it is the result of a procedure with good sampling characteristics*.

What kind of procedures are we talking about, and what characteristics of those procedures ought we to care about? The error statistical approach distinguishes itself from other frequentist frameworks (e.g., frequentist statistical decision theory) by the answer it gives to that question. Particular attention is paid to *tests*, by which I mean a procedure that takes some data and a statistical hypothesis as inputs and issues a binary pass/fail result. (As we’ll see, the testing framework easily encompasses estimation by holding the data input fixed and varying the statistical hypothesis input.) The error statistical worth of a test is related, sensibly enough, to the (in)frequency with which the test produces an erroneous conclusion, and, critically, what that error rate indicates about the capacity of the test to detect error *in the case at hand. *This notion is codified by the *Severity Principle*.

The most straightforward way to understand the Severity Principle (for me, anyway,) is as an extension of a rule of inference of classical logic that has the delightfully baroque name *modus tollendo tollens*, or more simply, *modus tollens*.

To apply *modus tollens*, one starts with two premises: first, “if *P*, then *Q*“; and second, “not-*Q*“. From these, *modus tollens* produces the conclusion “not-*P*“. *Modus tollens* is also known as *the law of contrapositive* because contraposition applied to the first premise yields “if not-*Q*, then not-*P*“.

For the purpose of exposition, I offer this slight reformulation of *modus tollens:* the two premises are “if not-*H*, then not-*P*” and “*P*“, and the conclusion is “*H*“. Here *H* represents an hypothesis and *P* represents a passing result from some test of *H*. The premise “if not-*H*, then not-*P*” expresses a property of the test, to wit, that it is incapable of producing an erroneous passing grade. The premise “*P*” expresses the assertion that for the observed data, the test procedure has produced a passing grade. In the language of error statistics, one says that *H* has passed a *maximally severe* test.

The above reformulation introduced the notion of a test into the premises, but because the first premise posited a perfect test, the whole idea of a test seemed rather superfluous. But classical logic is silent in the face of imperfect tests; and since learning from imperfect tests is, after all, possible, we seek an extension of *modus tollens* to imperfect tests.

The first step is to consider the opposite of a maximally severe test. Such a *minimally severe test* would be one gives a passing grade to *H* irrespective of the data. We can “frequencify” this notion: for a minimally severe test, we have

.

or equivalently,

(I use the symbol “Fr” to be clear that I’m writing about relative frequencies.) The analogous frequencification of a maximal severe test is

.

The equation in the above line captures only the first premise of *modus tollens*, so it’s a necessary but not sufficient component of the notion of a maximally severe test. To see this, notice that a procedure that always gives a failing grade to *H* irrespective of the data does satisfy the above equation; however, *modus tollens* will never apply. The inequality encodes the fact that part of what we *mean* by the word “test” is that it is at least possible to observe a passing grade, or to put it another way, that there must be some possible data that accords with *H.*

The key point is that the necessary conditions for a minimally and a maximally severe test are, respectively, Fr(not-*P* | not-*H*) = 0 and Fr(not-*P* | not-*H*) = 1. This suggests that (provided we’ve checked that Fr(*P* | *H*) > 0,) we can measure the severity of a test by the value of Fr(not-*P* | not-*H*) .

At this point, I’m just going to quote straight from Mayo’s latest exposition of severity:

“**Severity Principle** []. Data *x*_{0} (produced by process *G*) provides good evidence for hypothesis *H* (just) to the extent that test *T* severely passes *H* with *x*_{0}.

…

A hypothesis *H* passes a severe test *T* with data *x*_{0} if,

(S-1) *x*_{0} accords with *H*, (for a suitable notion of accordance) and

(S-2) with very high [frequency], test *T* would have produced a result

that accords less well with *H* than *x*_{0} does, if *H* were false or incorrect.”

My previous discussion was based on the idea of pass/fail testing, whereas condition (S-2) is phrased in terms of “accord[ing] less well”, the key word being “less”. Mayo’s definition does not merely introduce the notion of accordance with *H* — it demands a totally ordered set to express it.

To connect my exposition here with Mayo’s definition, we can now recognize that, just as school exams produce both a numerical grade and a pass/fail categorization, a statistical data-based pass/fail test will (almost always) be a dichotomization of a test statistic that makes finer distinctions, and the choice of dichotomization threshold is essentially arbitrary. Mayo’s definition of a severe test resolves this arbitrariness by placing the threshold for a passing grade right at the observed value of the test statistic. (The threshold is notionally infinitesimally below the observed value of the test statistic, so that *H* just barely passes. Alas, the reals contain no infinitesimals.)

To make the notion of the severity of a test *T* of *H* mathematically precise and operational, we’ll have to get more specific about what is meant by “accords less well”. That will be the topic of part two.* *

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Recall Cox’s five postulates:

*Cox-plausibilities are real numbers*.*Consistency with Boolean algebra*: if two claims are equal in Boolean algebra, then they have equal Cox-plausibility.- There exists a
*conjunction function**f*such that for any two claims*A, B,*and any prior information*X,*

.

- There exists a
*negation relation*(actually a function too). In slightly different notation that in the previous post, it is:

.

- The negation relation and conjunction function (and their domains) satisfy technical
*regularity**conditions.*

Choices other than the reals are possible: one might choose a domain with less structure, such as a lattice, or larger dimensionality, such as the set of real intervals as in Dempster-Shafer theory. At present, it seems to me that choosing one these other possibilities as the domain doesn’t buy us much in terms of usefulness for practical applications. That said, I could be swayed from this view by relevant evidence.

I doubt such evidence will be forthcoming. The reason is that the key property that distinguishes the reals from the other possible choices for the domain is that the reals are totally ordered. By making this choice, we ensure that the Cox-plausibilities of all the claims in whatever universe of discourse we’re considering will also be totally ordered. Conversely, if the domain is only a poset, then for at least one pair of claims, we won’t be able to pick the one with the larger plausibility (or state that they’re equally plausible).

This is not intrinsically a strike against posets as accurate representations of some set of available information — I acknowledge that a lack of universal comparability may indeed be quite appropriate in some settings. Rather, my intuition is that these settings are precisely the ones for which the paucity of prior information ensures that very little is actually achievable in practice.

This postulate says that the Cox-plausibility for a given Boolean expression depends on its truth table rather than the particular symbols used in the expression. Personally I have no qualms accepting this postulate, and it would surprise me if anyone found it controversial. Perhaps something interesting could be generated without this postulate, but I feel sure that any such development will not have semantics appropriate to plausibility.

I won’t give a full argument for the necessity of this particular form, but I will offer an example of the kind of reasoning that leads to it.

Instead of the conjunction function I gave above, suppose we consider

Can this possibly serve as the functional relationship between the the plausibility of a conjunction and the plausibility of the conjuncts?

It can’t. Consider the plausibility of the claim that some person, (say, the seventh person you encounter tomorrow) has blue eyes. This is a conjunction of the claim that the person has a blue left eye (*L _{B}*) and a blue right eye (

,

,

and so for any sufficiently regular *f*_{?},

.

But

so this functional form isn’t flexible enough to do the job we’d want it to do.

In a similar way, test cases can be defined and applied to all of the possible functional forms, of which there are a small number. Only two survive: the one I gave in postulate #3 and the one obtained from it by interchanging *B *and* A*.

Curiously, the literature did not contain a full account of such a test for quite some time; the full procedure was carried out in Whence the laws of probability? by A.J.M. Garrett.

Actually, there’s no real reason to separate negation and conjunction into separate postulates. The link immediately above is to a paper which uses NAND instead of conjunction and negation separately. It’s also possible to get to Cox’s theorem by considering conjunction and disjunction.

Cox’s original proof assumed that the conjunction function and negation relation were twice-differentiable; Jaynes offered a proof that assumed just differentiability. Mathematically speaking, these are quite strong assumptions; by using them, Cox and Jaynes left open the possibility of non-differentiable solutions.

Frankly, given my training as an engineer, I’m not too concerned that other, non-differentiable solutions might exist. I’d be happy to consider such solutions as they appear in the literature, but for me, the differentiable solution is enough to be going on with. But if you don’t share my cavalier attitude, be comforted, for you are not alone. Within the past 15 years or so, interest in the necessary assumptions for Cox’s theorem was revived by a paper of J. Y. Halpern purporting to give a counter-example to the theorem. The counter-example violated one of the regularity conditions Cox did in fact assume; Halpern acknowledged this and went on to argue that the necessary regularity conditions were nevertheless “not natural”.

This argument prompted a straight-up counterargument by K. S. Van Horn and also research into more natural regularity condtions. (The K. S. Van Horn paper is to my go-to link when referring to Cox’s theorem in blog comments; if you like what you’ve read here, read that next.) More recently, Frank J. Tipler (of *Omega Point* infamy) and a co-author have written a paper that assumes a lot of mathematical machinery with which I am not familiar and claims to give a “trivial” proof of Cox’s theorem. And very recently, K. Knuth and J. Skilling have offered an approach they call “simple and clear” and which they claim unites and extends the approaches of Kolmogorov and Cox.

Assuming, then, that somewhere in the morass of links above there exists a set of satisfactory postulates, where does that leave us? Let me characterize Cox’s theorem in three ways, two negative and one positive.

First off, *Cox’s theorem is not a straitjacket*. Unlike other approaches to Bayesian foundations, we made no loaded claims of rational behavior, preference, or, arguably, belief. We can jump into and out of any or all joint (over parameters/hypotheses and data) prior probability distributions we care to set up, examining the consequences of each in turn.

Second, *Cox’s theorem is not a guarantee of soundness*. Just as in classical logic, nothing in protects us from garbage-in-garbage-out. If we want to argue that the conclusions of a Bayesian analysis are well-warranted, we **must** justify the prior distributions we used in terms of the available prior information.

Finally, *Cox’s theorem is a guarantee of validity.* It justifies Bayes’ theorem as an objectively well-founded method for computing the plausibility of claims post-data given the plausibility of claims pre-data.

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I subscribe to a school of thought some call “Jaynesian” after Edwin T. Jaynes. Its foundation is a theorem of Richard T. Cox, a physicist who studied electric eels, not to be confused with the eminent statistician Sir David R. Cox. Since my first project will be to engage with Professor Mayo’s diametrically opposed views on the proper way to use (and think about the use of) statistics in science, it seems worthwhile to describe the theorem and the reasons I take it to be foundational to statistics — of the Bayesian variety, at least.

This section is somewhat disjointed; I chose conciseness and links over a well-written and complete introduction.

Cox sought to formalize the notion of the* plausibility of a claim*. (Following Professor Mayo, I use “claim” in preference to “assertion” or “proposition”.) The kinds of claims I’m talking about are those that admit two extremes of plausibility: these kinds of claims could either be known to be true, and thus be as plausible as it is possible to be; or they could be known to be false, and thus be as implausible as it is possible to be. In particular, I’m not talking about the kinds of claims that can still be under dispute once all the relevant facts are known, e.g., aesthetic or moral judgments.

Even in the times of antiquity, we knew how to guarantee that only true conclusions would be inferred from true premises. But absent any premises, the rules of that method — the syllogisms of Aristotelian logic — cannot operate; to get out something worthwhile, we have to provide worthwhile input. In likewise fashion, we need some background knowledge — oh heck, let’s just call it *prior information* — on which to base the assessment of the plausibility of a claim.

Boolean algebra provides rules for manipulating arbitrary combinations of conjunctions (), disjunctions (), and negations () of claims. (Such combinations are themselves claims). Actually, disjunction can be defined in terms of conjunction and negation, so Cox focused on the latter two operations.

So that’s the background. Next, I’ll give Cox’s postulates, a statement of the theorem, and a high-level overview of the proof. In the post following this one, I’ll discuss why I think the postulates are reasonable and how the resulting perspective guides my approach to statistics.

I’ll refer to quantities of the type considered by Cox as *Cox-plausibilities* to distinguish them the informal notion of plausibility. (Cox, writing in 1946, used the term “likelihood” which I will avoid for obvious reasons.) But first, I need some notation: upper-case letters will refer to claims; I’ll use *X* as the symbol for some generic prior information. For Cox-plausibilities I’ll use, e.g., the symbol *A|X* to represent the the (real-valued) Cox-plausibility of claim *A* evaluated on prior information *X*.

The following five postulates set out the properties that a system of Cox-plausibilities must have. They are:

*Cox-plausibilities are real numbers*.*Consistency with Boolean algebra*: if two claims are equal in Boolean algebra, then they have equal Cox-plausibility.- There exists a
*conjunction function**f*such that for any two claims*A, B,*and any prior information*X,*

.

In words, this postulate says that the Cox-plausibility of a conjunction is some function of (i) the Cox-plausibility of one of the conjuncts, and (ii) the Cox-plausibility of the other conjunct under the assumption that the first conjunct is true. I admit, it doesn’t look very compelling when just stated baldly.

- There exists a
*negation relation.*(Okay, it’s actually a function too.) For now I defer giving it a symbol; in words, it says that the Cox-plausibility of the negation of a claim is a function of the Cox-plausibility of the claim (all relative to the same prior information). - The negation relation and conjunction function (and their domains) satisfy technical
*regularity**conditions.*

Succinctly stated, Cox’s theorem is: *any system of Cox-plausibilities is isomorphic to probability*.

Conjunction is associative in Boolean algebra:

The consistency postulate (and the regularity conditions on the domain of the conjunction function) then require that the conjunction function obeys a functional equation sometimes called the Associativity Equation:

The Associativity Equation plus the regularity conditions imply that there must exist a strictly increasing invertible function *g* such that

This equation is significant enough to deserve its own name: it’s the *product rule*. Note that for the function *p,* defined as

the product rule still holds*.*

The negation relation can now be stated as: there exists a function *h* such that

Together, the consistency requirement, the product rule, and the negation relation yield another functional equation:

Invoking those regularity conditions again, the general solution of the above equation is

Stated in terms of *p*, the above equation is*:*

which can be rearranged to give the *sum rule:*

Taken together, the sum rule and product rule are the usual starting point for expositions of probability theory, so that’s the whole thing.

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Not every post will contribute to the completion of above agenda; I also plan to write posts sharing my thoughts on any interesting statistical topic I happen to run into. Posts appear below in reverse chronological order; scroll to the bottom for the first one.

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