Jaynes: Probability (2003), ch. 3

While discussing the probability of drawing the same ball twice when sampling with replacement from an urn, Jaynes breaks off into a little "sermon" (pp. 64–66):

In probability theory there is a very clever trick for handling a problem that becomes too difficult. We just solve it anyway by:

1. Making it still harder;
2. Redefining what we mean by “solving” it, so that it becomes something we can do;
3. Inventing a dignified and technical-sounding word to describe this procedure, which has the psychological effect of concealing the real nature of what we have done, and making it appear respectable.

In the case of sampling with replacement, we apply this strategy by

1. Supposing that after tossing the ball in, we shake up the urn. However complicated the problem was initially, it now becomes many orders of magnitude more complicated, because the solution now depends on every detail of the precise way we shake it, in addition to all the factors mentioned above;
2. Asserting that the shaking has somehow made all these details irrelevant, so that the problem reverts back to the simple one where the Bernoulli Urn Rule applies;
3. Inventing the dignified-sounding word randomization to describe what we have done. This term is, evidently, a euphemism whose real meaning is: deliberately throwing away relevant information when it becomes too complicated for us to handle. (p. 64)

Just to be sure, he adds:

Shaking does not make the result “random,” because that term is basically meaningless as an attribute of the real world; it has no clear definition applicable in the real world. (p. 65)

I think I would agree with Jaynes that randomization in field experiments is akin to a protective ritual. To the extent that such a tirual is intended to protect us against a malicious Nature out to get us, it is absurd.

But like the proponents of randomized trials, Jaynes here fails to see that the evil adversary might in fact be a dishonest experimenter rather than a malicious Nature. Both of these characters are in principle vulnerable to strategies like randomization, but unlike Evil Nature, Evil Scientist actually exists.

Edwards on Fisher (2005)

In his discussion of Fisher's 1925 book Statistical Methods for Research Workers, Edwards writes:

It was not until 1950 that the word ‘Bayesian’ was coined, by Fisher himself, to refer to inverse probability (p. 862)

Can this really be true? To be sure, "inverse probability" was the more common term before 1950, but was "Bayesian" really never used, at all?

I thought this claim would not stand up to 30 seconds of googling, but I was wrong. The only reference I've found so far is from the bibliography in Jimmy Savage's Lecture Notes on Mathematical Statistics, which includes the following item:

Jeffreys, Harold. Theory of Probability. New York: Oxford University Press, 1939. 380 pp. A highly controversial book on the philosophical foundations of statistics by the most foremost modern exponent of the Bayesian heresy. Examples largely from geophysics.

I don't have access to Savage's book here, so I can't vouch for the year of publication, but Amazon, WorldCat, Google Books, and a few other resources all give the date as 1947.

If that's true, then the word "Bayesian" was used at least once before 1950. But one is certainly not a crowd.

Edwards: Likelihood (1972)

Edwards (from his Cambridge site)

The geneticist A. F. W. Edwards is a (now retired) professor of biometry who was massively influenced by Ronald Fisher in his scientific writings. His books Likelihood argues that the likelihood concept is the only sound basis for scientific inference, but it reads at times almost like one long rant against Bayesian statistics (particularly ch. 4) and Neyman-Pearson theory (particularly ch. 9).

Don't Do Probs

As an alternative to these approaches to statistics, Edwards proposes that we limit ourselves to makes assertions only in terms of likelihood, "support" (log-likelihood, p.12), and likelihood ratios. In the brief epilogue of the book, he states that this

… allows us to do most of the things which we want to do, whilst restraining us from doing some things which, perhaps, we should not do. (p. 212)

In particular, this approach emphatically prohibits the comparison of hypotheses in probabilitistic terms. The kind of uncertainty we have about scientific theories is simply not, Edwards states, of a nature that can be quantified in terms of probabilities: "The beliefs are of a different kind," and they are "not commensurate" (p. 53)

The Difference Between Bad and Worse

He briefly mentions Ramsey and his Dutch book-style argument for the calculus of probability, and then goes on to speculate that, had not died so young,

… perhaps he would have argued that his demonstration that absolute degrees of belief in propositions must, for consistency's sake, obey the law of probability, did not compel anyone to apply such a theory to scientific hypotheses. Should they decline to do so (as I do), then they might consider a theory of relative degrees of belief, such as likelihood supplies. (p. 28)

In other words, it might be true that you cannot assign numbers to propositions in any other way than according to the calculus of probabilities, but you can always reject to have a quantitative opinion in the first place (or not make a bet).

Nulls Only

Consistently with Fisher's approach to statistics, Edwards finds it important to distinguish between null and not-null hypotheses: That is, in opposition to Neyman-Pearson theory, he refuses to explicitly formulate the alternative hypothesis against which a chance hypothesis is tested.

Here as elsewhere, this is a serious limitation with quite profound consequences:

It should be noted that the class of hypotheses we call 'statistical' is not necessarily closed with respect to the logical operations of alternation ('or') and negation ('not'). For a hypothesis resulting from either of these operations is likely to be composite, and composite hypotheses do not have well-defined statistical consequences, because the probabilities of occurrence of the component simple hypotheses are undefined. For example, if $p$ is the parameter of a binomial model, about which inferences are to be made from some particular binomial results, '$p=\frac{1}{2}$' is a statistical hypothesis because its consequences are well-defined in probability terms, but its negation, '$p\neq\frac{1}{2}$', is not a statistical hypothesis, its consequences being ill-defined. Similarly, '$p=\frac{1}{4}$ or $p=\frac{1}{2}$' is not a statistical hypothesis, except in the trivial case of each simple hypothesis having identical consequences. (p. 5)

This should also be contrasted with Jeffreys' approach, in which the alternative hypothesis has a free parameter and thus is allowed to 'learn', while the null has the parameter fixed at a certain value.

Scientists With Attitude

At several points, in the book, Edwards uses the concerns of the working scientist as an argument in favor of a likelihood-based reasoning calculus. He thus faults Bayesian statistics for "fail[ing] to answer questions of the type many scientists ask" (p. 54).

This question, I presume, is "What does the data tell my about my hypotheses?" This is distinct from "What should I do?" or "Which of these hypotheses is correct?" in that it only supplies the objective, quantitative measure of support, not the conclusion:

The scientist must be the judge of his own hypotheses, not the statistician. The perpetual sniping which statisticians suffer at the hands of practising scientists is largely due to their collective arrogance in presuming to direct the scientists in his consideration of hypotheses; the best contribution they can make is to provide some measure of 'support', and the failure of all but a few to admit the weaknesses of the conventional approaches has not improved the scientists' opinion. (p. 34)

In brief form, this leads to the following tirade against Bayesian statistics:

Inverse probability, in its various forms, is considered and rejected on the grounds of logic (concerning the representation of ignorance), utility (it does not allow answers in the form desired), oversimplicity (in problems involving the treatment of frequency probabilities) and inconsistency (in the allocation of prior probability distributions). (p. 67–68)

Fisher: The Design of Experiments (4th ed., 1947), Chapter I

Fisher; from Judea Pearl's website.

Now, here's a revealing turn of phrase:

In the foregoing paragraphs the subject-matter of this book has been regarded from the point of view of an experimenter, who wishes to carry out his work competently, and having done so wishes to safeguard his results, so far as they are validly established, from ignorant criticism by different sorts of superior persons. (p. 3)

You could hardly spell out more explicitly the philosophy that lies behind Fisher's concept of statistics: It's a strategic ritual, not designed to ensure a result, but to protect against criticism.

Perfectly Rigorous and Unequivocal

Such protection only goes as far as the mathematical consensus on the validity of the logic. But Fisher goes on to state that "rigorous deductive argument" is possible even in the context of random events, citing gambling as a proof of concept:

The mere fact that inductive inferences are uncertain cannot, therefore, by accepted as precluding perfectly rigorous and unequivocal inference. (p. 4)

This seems to confuse the issues of probability and statistics, unless his argument here really only amounts to saying that distributions are non-stochastic entities.

Useless for Scientific Purposes

This leads him to a discussion of "inverse probability," which he gives three reasons for rejecting: First,

… advocates of inverse probability seem forced to regard mathematical probability, not as an objective quantity measured by observed frequencies, but as measuring merely psychological tendencies, theorems respecting which are useless for scientific purposes. (p. 6–7)

Second, Bayes' axiom (about the flat prior for a coin flip) is not self-evident, that is, the choice of prior is not unequivocal (p. 7).

Ever Since the Dawn of Man…

And third,

… inverse probability has been only very rarely used in the justification of conclusions from experimental facts, although the theory has been widely taught, and is widespread in the literature of probability. Whatever the reasons are which could give experimenters confidence that they can draw valid conclusions from their results, they seem to act just as powerfully whether the experimenter has heard of the theory of inverse probability or not. (p. 7)

That's a funny sociological proof, given that he has just rejected Bayesian statistics for its psychologism. But he himself sometimes seems to think that his statistics is a kind of theory of learning, whatever that means:

Men have always been capable of some mental processes of the kind we call "learning by experience." … Experimental observations are only experience carefully planned in advance, and designed to form a secure basis of new knowledge; (p. 8)

Fisher: Statistical Methods and Scientific Inference (1956), chapter 5.7

In chapter V of his book on statistical inference, Fisher compares various likelihood-based approaches to coming up with a predictive distribution. Some of the details are quite obscure, and I have problems following his argument in several places.

Section 2 is dedicated to to the Bayesian solution for a series of coin flips. It contains, among other things, a strange reference to coefficients other than the binomials, suggesting that these can be replaced freely with any other suitable polynomial (p. 112). I am not quite sure what he means or how he imagines this should be justified.

Section 7 is dedicated to a particular type of frequentist prediction. The set-up is that we have observed the counts a and b (heads and tails) and that we would like to find the likelihood of a continuation having counts c and d.

In order to find this, he suggests that we compute the likelihood ratio

Pr(a, b | f) Pr(c, d | f) / Pr(a + c, b + d | f).

The logic behind this computation is that a/b is close to c/d, then the joint probability of those two ratios is approximately the same as the probability of the pooled ratio (a + c)/(b + d). If, on the other hand, they both deviate highly from the maximum likelihood estimate (in different directions), then the joint probability will be lower than the pooled reference value. However, the actual value of the parameter of the coin flip cancels out from the fraction and thus plays no direct role in the computation.

Fisher goes through an example in which a = 3, b = 16, c = 14, d = 7. In order to compute the many factorials for this example, he uses the (very rough) approximation

x! ≈ x^x.

Or at least that's what I think he does — he comments that this x^x is "among others having the same margins," whatever that is supposed to mean (p. 129).

N! (green) and the approximation N^N (red).

At any rate, we can redo his computation using both his own approximate method and the exact formula, getting a likelihood of about .004 (Fisher's result) or .001 (the exact result).

As he suggests on page 130, we can also compile a table of likelihoods for various other values of c and d adding to 21. We can collect all of these results in a table like the following:

Count Fisher Exact Bayes 0 .094 .098 .048 1 .0499 .223 .109 2 .0836 .309 .151 3 .991 .336 .164 4 .964 .311 .152 5 .817 .256 .125 6 .621 .192 .094 7 .432 .133 .065 8 .277 .085 .042 9 .164 .051 .025 10 .090 .028 .014 11 .046 .015 .007 12 .022 .007 .003 13 .009 .003 .002 14 .004 .001 .001 15 .001 .000 .000 16 .000 .000 .000 … … … … Sum 5.867 2.050 1.000

As the table shows, the exact likelihoods coincide with the Bayes estimates if we normalize them. I think this is only the case because the numbers are large enough because of an issue with the normalizing constants in a Dirichlet distribution, but I don't have time to check the details now.

Fisher: "On the Mathematical Foundations of Theoretical Statistics" (1921)

I haven't had time to study this paper in detail yet, but based on a quick skim, it seems that Fisher

• criticizes Bayesian statistics on the grounds that it is sensitive to reparametrizations of the hypothesis space;
• emphasizes the concept of likelihood and its differences from probability;
• presents, justifies, and illustrates the concept of Fisher information. 

I'll read the whole thing later. But for now, a few quotes.

First, a centerpiece in Bayes' original paper was the postulate that the uncertainty about the bias of a coin should be represented by means of a uniform distribution. Fisher comments:

The postulate would, if true, be of great importance in bringing an immense variety of questions within the domain of probability. It is, however, evidently extremely arbitrary. Apart from evolving a vitally important piece of knowledge, that of the exact form of the distribution of values of p, out of an assumption of complete ignorance, it is not even a unique solution. (p. 325)

Second Bayesian topic is ratio tests: That is, assigning probabilities to two exclusive and exhaustive hypotheses X and Y based on the ratio between how well they explain the data set A, that is,

Fisher in 1931; image from the National Portrait Gallery.

Pr(A | X) / Pr(A | Y).

Fisher comments:

This amounts to assuming that before A was observed, it was known that our universe had been selected at random for [= from] an infinite population in which X was true in one half, and Y true in the other half. Clearly such an assumption is entirely arbitrary, nor has any method been put forward by which such assumptions can be made even with consistent uniqueness. (p. 326)

The introduction of the likelihood concept:

There would be no need to emphasise the baseless character of the assumptions made under the titles of inverse probability and BAYES' Theorem in view of the decisive criticism to which they have been exposed at the hands of BOOLE, VENN, and CHRYSTAL, were it not for the fact that the older writers, such as LAPLACE and POISSON, who accepted these assumptions, also laid the foundations of the modern theory of statistics, and have introduced into their discussions of this subject ideas of a similar character. I must indeed plead guilty in my original statement of the Method of the Maximum Likelihood (9) to having based my argument upon the principle of inverse probability; in the same paper, it is true, I emphasised the fact that such inverse probabilities were relative only. That is to say, that while we might speak of one value of p as having an inverse probability three times that of another value of p, we might on no account introduce the differential element dp, so as to be able to say that it was three times as probable that p should lie in one rather than the other of two equal elements. Upon consideration, therefore, I perceive that the word probability is wrongly used in such a connection: probability is a ratio of frequencies, and about the frequencies of such values we can know nothing whatever. We must return to the actual fact that one value of p, of the frequency of which we know nothing, would yield the observed result three times as frequently as would another value of p. If we need a word to characterise this relative property of different values of p, I suggest that we may speak without confusion of the likelihood of one value of p being thrice the likelihood of another, bearing always in mind that likelihood is not here used loosely as a synonym of probability, but simply to express the relative frequencies with which such values of the hypothetical quantity p would in fact yield the observed sample. (p. 326)

In the conclusion, he says that likelihood and probability are "two radically distinct concepts, both of importance in influencing our judgment," but "confused under the single name of probability" (p. 367) Note that these concepts are "influencing our judgment" — that is, they are not just computational methods for making a decision, but rather a kind of model of a rational mind.

Zabell: "R. A. Fisher and the Fiducial Argument" (1992)

Chapter 3.3 of Fisher's 1956 book is dedicated to his so-called "Fiducial Argument."

I was extremely confused by his presentation and looked around for some secondary literature. This brought me to this wonderful paper by Sandy Zabell, which explains how Fisher's ideas about fiducial inference were indeed quite confused and changed a lot over time. It also explains the core of his argument better than he did himself (to my mind, at least).

As I now understand Fisher's argument, this is the idea: When you have a statistical model with a flat prior, the posterior probability of a specific parameter setting is proportional to the likelihood of the data under that parameter setting,

Pr(p | x) ∝ Pr(x | p)

However, for many unbounded parameter spaces, the likelihood Pr(X = x | p) does not have a finite integral when considered as a function of p. In such cases, a straightforward use of Bayesian inference with a flat prior is not an option.

But, Fisher says, consider instead the cumulative likelihood Pr(X < x | p). This is a function of x which always lies between 0 and 1, and it is 0 at negative infinity and 1 at positive infinity.

Pr(X < x | p) for uniform distributions with right end-points p = 3, p = 5, and p = 7.

The trick now is to view this cumulative likelihood as a function of p instead of a function of x. In many but not all cases, this function will be 1 when the parameter is at negative infinity and 0 when it is at positive infinity.

Cumulative likelihood at x = 1.5, x = 2.5, and p = 3.5 as a function of the parameter.

For instance, if p is the mean of a normal distribution, the cumulative likelihood Pr(X < x | p) decreases in this way. The reason is that the upper bound x stays where it is, while the expected value of the variable increases.

Uniform likelihoods Pr(X < x | p) with varying right end-points p.

In such cases, we can thus interpret the cumulative likelihood as the complement of a CDF for the parameter,

G(p) = 1 – Pr(X < x | p).

If this function G is differentiable, we can further interpret G' as a PDF for the parameter p given observation x.

As an example, suppose (as on the pictures) that a number X is drawn from a uniform distribution on the interval [0, p]. The cumulative likelihood is then

Pr(X < x | p) = x/p    (0 < x < p),

and 0 and 1 below and above the interval, respectively.

Fiducial PDFs given the observations x = 1.5, x = 2.5, and x = 3.5.

Considering the complement of this function, 1 – x/p, as a CDF for the parameter p, we can differentiate it in order to get the density

G'(p) = x/p²    (x < p),

when p > x and 0 otherwise. We have thus obtained a posterior probability distribution for the parameter without assuming anything about the prior.

It should be noted that

• This method does not always work; consider for instance the case in which the cumulative likelihood oscillates between a unimodal normal and a bimodal normal distribution as the parameters runs along the real number line.
• The method can also give inconsistent results; for instance, the fiducial distribution of X² is, as far as I understand, not necessarily the distribution you would get by finding the fiducial distribution of X and then deriving a distribution for X².
• The method has no single, natural extension to the multi-parameter case, and there are some serious obstacles to constructing such an extension.

It is also interesting that in the example above, the fiducial distribution corresponds to the posterior you get if you assume the improper prior 1/p. It can thus not be rationalized as a posterior inference using only ordinary probability distributions, but it can if we allow ourselves crazy, unnormalizable ones.

Fisher: "Statistical Methods and Scientific Induction" (1955)

Ronald Fisher; image from Wikimedia Commons.

In this brief paper, Sir Ronald Fisher militates against what he sees as wrong and absurd interpretations of the notion of a statistical test.

The Ideology of Statistics

The core of his argument is that a test only gives positive information when yields a significant difference and thus warrants the rejection of a hypothesis — an absence of a significant difference does not mean "accept." He contends that

… this difference in point of view originated when Neyman, thinking that he was correcting and improving my own early work on tests of significance, … in fact reinterpreted them in terms of that technological and commercial apparatus which is known as an acceptance procedure. (p. 69)

And although acceptance procedures might be good enough for commerce, they have no place in science:

I am casting no contempt on acceptance procedures, and I am thankful, whenever I travel by air, that the high level of precision and reliability required can really be achieved by such means. But the logical differences between such an operation and the work of scientific discovery by physical or biological experimentation seem to me so wide that the analogy between them is not helpful, and the identification of the two sorts of operation is decidedly misleading. (pp. 69–70)

Then comes the juicy part:

I shall hope to bring out some of the logical differences more distinctly, but there is also, I fancy, in the background an ideological difference. Russians are made familiar with the ideal that research in pure science can and should be geared to technological performance, in the comprehensive organized effort of a five-year plan for the nation. How far, within such a system, personal and individual inferences from observed facts are permissible we do not know, but it may be safer, and even, in such a political atmosphere, more agreeable, to regard one's scientific work simply as a contributary element in a great machine, and to conceal rather than to advertise the selfish and perhaps heretical aim of understanding for oneself the scientific situation. In the U.S. also the great importance of organized technology has I think made it easy to confuse the process appropriate for drawing correct conclusions, with those aimed rather at, let us say, speeding production, or saving money. There is therefore something to be gained by at least being being able to think of our scientific problems in a language distinct from that of technological efficiency. (p. 70)

So there you have it: In the technological regime of either of the two Cold War superpowers, "learning," "inference," and private, inner thought are taboo, according to Fisher. Presumably we are to contrast this with the aims of British science going back to Newton.

The Three Issues

Fisher singles out three phrases that he finds particularly offensive in scientific statistics:

1. "Repeated sampling from the same distribution"
2. Errors of the "second kind"
3. "Inductive behaviour"

I'll discuss these one by one.

1. "Repeated sampling from the same distribution"

The issue with the first one is not completely clear to me, but here is what I make of his discussion (pp. 71–72): Suppose you are performing a test to see whether the mean of some population has a specific value; suppose further that the standard deviation of that population is unknown, but that you have estimated it based on the available sample.

The problem then is, if I understand Fisher correctly, that the test depends on the standard deviation being constant and known, but in reality, it is an unknown quantity that you have estimated by a maximum likelihood method. This is, strictly speaking, illegitimate, since any estimate should be based on a numerous and representative sample; but since the standard deviation is a property of samples of size N, you should really have M samples of a sample of size N in order to have some data to estimate from. But clearly, this sets a far too high standard for the amount of data required.

It's a convoluted argument, but I think it makes sense from a rigorously frequentist standpoint: If parameters are consistently interpreted as frequencies, then the only legitimate statistical procedure for learning about an unknown quantity t is to obtain a large number of samples dependent on t and then wait for the law of large numbers to kick in.

Strictly speaking, this means that the amount of data points you need in order to estimate all the parameters in a model will grow exponentially in the number of parameters. That sounds sort of crazy, but if you do not allow yourself to have any model in the absence of data, you really have to wait for the data to overwhelm your initial ignorance before you can say that you have a model of the situation. That takes time.

2. Errors of the "Second Kind"

Errors of the first kind are false negatives: Cases in which, for instance, a population in fact has mean m, but nevertheless exhibits a sample average so far away from m that the hypothesis is rejected. Such errors have a frequentist interpretation, because the likelihoods given m are well-defined even in the absence of a prior distribution over m.

Errors of the second kind are false positives: Some other mean m' different from m produces a sample average so close to m that the false hypothesis of a mean of m is confirmed. This kind of error has no frequentist interpretation, because it requires the alternative hypotheses m' to have prior probabilities, and because it requires that there be a loss function associated with accepting the hypothesis of m when the true mean m' is close to m.

Jerzy Neyman in the classroom, 1973; image from Wikimedia Commons.

Fisher is not willing to assume any of those two instruments. He writes:

It was only when the relation between a test of significance and its corresponding null hypothesis was confused with an acceptance procedure that it seemed suitable to distinguish errors in which the hypothesis is rejected wrongly, from errors in which it is "accepted wrongly" as the phrase does. (p. 73)

Such language is not just scientifically irresponsible, he thinks — it also misunderstands the private states of mind present in the head of a scientist:

The fashion of speaking of a null hypothesis as "accepted when false", whenever a test of significance gives us no strong reason for rejecting it, and when in fact it is in some way imperfect, shows real ignorance of the research worker's attitude, by suggesting that in such a case he has come to an irreversible decision. (p. 73; Fisher's emphasis)

Of course, neither positive nor negative decisions are immune to revision as more data comes in (cf. p. 76), so Fisher prefers to depict the scientist's attitude as one of cautious learning in the face of data. This contrasts with the forced-choice nature of acceptance procedures:

In an acceptance procedure, on the other hand, acceptance is irreversible, whether the evidence for it was strong or weak. It is the result of applying mechanically rules laid down in advance; no thought is given to the particular case, and the tester's state of mind, or his capacity for learning, is inoperative.

By contrast, conclusions drawn by a scientific worker from a test of significance are provisional, and involve an intelligent attempt to understand the experimental situation. (pp. 73–74; Fisher's emphasis).

Note again the insistence on private states of mind as the hallmark of scientific rationality.

3. "Inductive Behaviour"

The last issue Fisher has with Neyman's brand of statistics is shelves under the heading above, but it is really about an issue of linguistics: Neyman contends (according to Fisher's summary — there is no direct reference) that statements like

There is 5% probability that the sample average deviates strongly from the mean

have a meaningful and well-defined interpretation (in terms of likelihood). On the other hand,

There is 5% probability that the mean deviates strongly from the sample average

is meaningless, because the mean is not a random variable.

Fisher disagrees, not because he is a fan of prior probability distributions on the parameters, but because he thinks that such statements could only ever refer to likelihoods. To make this point vivid, he considers (I am changing the example a bit here) a statement of the form

Pr(m < x) = 5%,

where m is a parameter and x is an observation, and he contrasts this with

Pr(m < 17) = 5%.

If one of these statements has a meaning, he says, clearly the other one must have a meaning too, unless we want to "deny the syllogistic process of making a substitution" (p. 75). But Neyman contends that the probability of a statement of the second kind should be "necessarily either 0 or 1" (p. 75), so that only the former probability (the likelihood given the mean) is well-defined.

Fisher comments:

The paradox is rather childish, for it requires that we should wilfully misinterpret the probability statement so as to pretend that the population to which it refers is not defined by our observations and their precision, but is absolutely independent of them. (p. 75)

By this he means that the reference class (the "population") is defined arbitrarily by our experimental set-up. And as he says about populations earlier in the paper, "no one of them has objective reality, all being products of the statistician's imagination" (p. 71).

An Englishman's Duty

In the conclusion, Fisher comes back to the ethical standards of statistics:

As an act of construction the hypothesis is not altogether impersonal, for the scientist's personal capacity for theorizing comes into it; moreover, the criteria by which it is approved require a certain honesty, or integrity, in their application. (p. 75)

Again, he explains that decision-theoretic methods (such as Bayesian statistics) have no business in scientific inference, since the goal is not optimal decisions, but the attainment of truth:

Finally, in inductive inference we introduce no cost functions for faulty judgments … In fact, scientific research is not geared to maximize the profits of any particular organization, but is rather an attempt to improve public knowledge undertaken as an act of faith to the effect that, as more becomes known, or more surely known, the intelligent pursuit of a great variety of aims, by a great variety of men, and groups of men, will be facilitated. We make no attempt to evaluate these consequences, and do not assume that they are capable of evaluation in any sort of currency.

… We aim, in fact, at methods of inference which should be equally convincing to all rational minds, irrespective of any intentions they may have in utilizing the knowledge inferred.

We have the duty of formulating, of summarizing, and of communicating our conclusions, in intelligible form, in recognition of the right or other free minds to utilize them in making their own decisions. (p. 77)

We could hardly have it more explicit: The difference in statistical paradigm is one of ethics.