Invited talk at the XVIII International Workshop on Maximum Entropy and Bayesian Methods (Maxent98), Garching / München (Germany), July 27-31 1998. physics/9811046
Abstract. The intuitive reasoning of physicists in conditions of uncertainty is closer to the Bayesian approach than to the frequentist ideas taught at University and which are considered the reference framework for handling statistical problems. The combination of intuition and conventional statistics allows practitioners to get results which are very close, both in meaning and in numerical value, to those obtainable by Bayesian methods, at least in simple routine applications. There are, however, cases in which ``arbitrary'' probability inversions produce unacceptable or misleading results and in these cases the conscious application of Bayesian reasoning becomes crucial. Starting from these considerations, I will finally comment on the often debated question: ``is there any chance that all physicists will become Bayesian?''
Key words: Subjective Bayesian Theory, High Energy Physics, Measurement Uncertainty
INTRODUCTION
MEASUREMENT UNCERTAINTY
PROFESSED FREQUENTISM VERSUS PRACTICED SUBJECTIVISM
HEP physicists ``are frequentist''
HEP physicists ``are Bayesian''
Intuitive application of Bayes' theorem
Bayes versus Monte Carlo
EXPLICIT USE OF BAYESIAN METHODS IN HEP
EXAMPLES OF MISLEADING RESULTS INDUCED BY
CONVENTIONAL STATISTICS
Claims of new physics based on p-values
What does a lower mass bound mean?
CONCLUSIONS
REFERENCES
High Energy Physics
(HEP) is well known for using
very sophisticated detectors,
status of the art computers, ultra-fast data acquisition systems,
and very detailed (Monte Carlo) simulations. One might imagine
that a similar level of refinement
could be found in its analysis tools, on the trail of
the progress in probability theory and statistics of the
past half century. Quite the contrary! As pointed out by
the downhearted Zech
[1],
``some decades ago physicists were usually well educated
in basic statistics in contrast to their colleagues in social and
medical sciences. Today the situation is almost reversed.
Very sophisticated methods are used in these disciplines, whereas
in particle physics standard analysis tools available in many program
packages seem to make knowledge of statistics obsolete. This leads
to strange habits, like the determination of a r.m.s. of a sample
through a fit to a Gaussian. More severe are a widely spread
ignorance about the (lack of) significance of
2
tests with a large number of bins and missing experience
with unfolding methods''. In my opinion, the main reason
for this cultural gap is that statistics and probability are not given
sufficient importance in the student curricula: ad hoc formulae
are provided in laboratory courses to report the ``errors'' of measurements;
the few regular lectures on ``statistics'' usually mix up
descriptive statistics, probability theory and
inferential statistics.
This leaves a lot of freedom for personal interpretations of the
subject (nothing to do with subjective probability!).
Of equal significance is the fact that
the disturbing catalog of inconsistencies
[2]
of ``conventional'' (1)
statistics helps to give the impression that this subject is matter of
initiates and local gurus, rather than a scientific
discipline (2) .
The result is that standard knowledge of statistics at
the end of the University curriculum is insufficient and confused,
as widely recognized. Typical effects of this (dis-)education are the
``Gaussian syndrome''
(3)
(from which follows the uncritical use of the rule of combining results,
weighing them with inverse of the ``error'' squared
(4) ,
or the habit of calling 2
any sum of squared differences between fitted curves and data points,
and to use it as if it were a
2),
the abused ``
n rule''
to evaluate ``errors'' of counting experiments
(5)
and the reluctance to take into account correlations
(6) ,
just to remain at a very basic level.
I don't think that researchers in medical science or in biology have a better statistics education than physicists. On the contrary, their usually scant knowledge of the subject forces them to collaborate with professional statisticians, and this is the reason why statistics journals contain plenty of papers in which sophisticated methods are developed to solve complicated problems in the aforementioned fields. Physicists, especially in HEP, tend to be more autonomous, because of their skills in mathematics and computing, plus of a good dose of intuition. But one has to admit that it is rather unlikely that a physicist, in a constant hurry to publish results before anybody else, can reinvent methods which have been reached by others after years of work and discussion. Even those physicists who are considered experts in statistics usually read books and papers written and refereed by other physicists. The HEP community remains, therefore, isolated with respect to the mainstream of research in probability and statistics.
In this paper I will not try to review all possible methods used in HEP, nor to make a detailed comparison between conventional and Bayesian solutions to solve the same problems. Those interested in this kind of statistical and historical study are recommended to look at the HEP databases and electronic archives [5]. I think that the participants in this workshop are more interested in learning about the attitude of HEP physicists towards the fundamental aspects of probability, in which framework they make uncertainty statements, how subjective probability is perceived, and so on. The intention here will be, finally, to contribute to the debate around the question ``Why isn't everybody a Bayesian'' [2], recently turned into ``Why isn't every physicist a Bayesian'' [6]. The theses which I will try to defend are:
Some of the points sketched quickly in this paper are discussed in detail in lecture notes [7] based on several seminars and minicourses given over the past years. These notes also contain plenty of general and HEP inspired applications.
1 I prefer to call the frequentist approach ``conventional'' rather than ``classical''. Back.
2 Who can have failed to experience endless discussions about trivial statistical problems, the solution of which was finally accepted just because of the (scientific or, more often, political) authority of somebody, rather than because of the strength of the logical arguments? Back.
3 I know a senior physicist who used to teach students that standard deviation is meaningful only for the Gaussian, and that it is ``defined'' as half of the interval around the average which contains 68% of the events! More common is the evaluation of the standard deviation of a data sample fitting a Gaussian to the data histogram (see also the previous quotation of Zech [1]), even in those cases in which the histogram has nothing to do with a Gaussian. The most absurd case I have heard of is that of someone fitting a Gaussian to a histogram exhibiting a flat shape (and having good reasons for being considered to come from coming from a uniform distribution) to find the resolution of a silicon strip detector!. Back.
4 For instance, the 1998 issue of the Review of Particle Physics [3] includes an example based on this kind of mistake with the intention to show that ``the Bayesian methodology ...is not appropriate for the objective presentation of experimental data'' (section 29.6.2, pag. 175). Back.
5 Who has never come across somebody
calculating the ``error'' on the efficiency
= n / N, using
the standard ``error propagation'' starting from
n
and N ?
Back.
6 In the past, the correlation matrix was for many HEP physicists ``that mysterious list of numbers printed out by MINUIT'' (MINUIT [4] is the minimization/fitting package mostly used in HEP), but at least some cared about understanding what those numbers meant and how to use them in further analysis. Currently - I agree with Zech [1] - the situation has worsened: although many people do take into account correlations, especially in combined analysis of crucial Standard Model parameters, the interactive packages, which display only standard deviations of fitted parameters, tend to ``hide'' the existence of correlations to average users. Back.
An idea well rooted among physicists, especially nuclear and particle physicists, is that the result of a measurement must be reported with a corresponding uncertainty. What makes the measured values subject to a degree of uncertainty is, it is commonly said, the effect of unavoidable measurement errors, usually classified as random (or statistical) and systematic (7) .
Uncertainties due to statistical errors are commonly treated using the frequentist concept of confidence intervals, although the procedure is so unnatural that the interpretation of the result is unconsciously subjective (as will be shown in a while), and there are known cases (of great relevance in frontier research) in which this approach is not applicable.
As far as uncertainties due to systematics errors are concerned, there is no conventional consistent theory to handle them, as is also indirectly recognized by the ISO Guide [10]. The ``fashion'' at the moment is to add them quadratically if they are considered to be independent, or to build a covariance matrix if not. This procedure is not justified theoretically (in the frequentist approach) and I think that it is used essentially because of the reluctance of experimentalists to add linearly the dozens of contributions of a complicated HEP measurement, as the old fashioned ``theory'' of maximum errors suggests doing (8) . The pragmatic justification for the quadratic combination of ``systematic errors'' is that one is using a rule (the famous ``error propagation'' formula (9) ) which is considered to be valid at least for ``statistical errors''. But, in reality, this too is not correct. The use of this formula is again arbitrary in the case of ``statistical errors'', if these have been evaluated from confidence intervals (10) . In fact, there is no logical reason why a probabilistic procedure proved for standard deviations of random variables (the observables) should also be valid for 68% confidence intervals, which is considered, somehow, an uncertainty attributed to the true value.
These examples show quite well the contradiction between the cultural background on probability and the practical good sense of physicists. Thanks to this good sense, frequentist ideas are constantly violated, with the positive effect that at least some results are obtained (11) . It is interesting to notice that in simple routine applications these results are very close, both in value and in meaning, to those achievable starting from what I consider to be the correct point of view for handling uncertainty (subjective probability). There are, on the other hand, critical cases in which scientific conclusions may be seriously mistaken. Before discussing these cases, let us look more closely at the terms of the claimed contradiction.
7 This last statement may sound like a tautology, since ``error'' and ``uncertainty'' are often used as synonyms. This hints to the fact that in this subject there is neither uniformity of language, nor of methods, as is recognized by the metrological organizations, which have made great efforts to bring some order into the field [8, 9, 10, 11, 12]. In particular, the International Organization for Standardization (ISO) has published ``Guide to the expression of uncertainty in measurement'' [10], containing definitions, recommendations and practical examples. For example, error is defined as ``the result of a measurement minus a true value of the measurand'' uncertainty ``a parameter, associated with the result of a measurement, that characterize the dispersion of the values that could reasonably be attributed to measurand'', and, finally, true value ``a value compatible with the definition of the given particular quantity''. One can easily see that it is not just a question of practical definitions. It seems to me that there is a well-thought-out philosophical choice behind these definitions, although it is not discussed extensively in the Guide. Two issues in the Guide that I find of particular importance are the discussion on the sources of uncertainty and the admission that all contributions to the uncertainty are of a probabilistic nature. The latter is strictly related to the subjective interpretation of probability, as admitted by the Guide and discussed in depth in [7]. (The reason why these comments on the ISO Guide have been placed in this long footnote is that, unfortunately, the Guide is not yet known in the HEP community and, therefore, has no influence on the behaviour of HEP physicists about which I am going to comment here. This is also the reason why I will often use in this paper typical expressions currently used in HEP and which are in disagreement with the ISO recommendations. But I will use these expressions preferably within quote marks, like ``systematic error'' instead of ``uncertainty due to a recognized systematic error of unknown size''.) Back.
8 In fact, one can see that when there are only 2 or 3 contributions to the ``systematic error'', there are still people who prefer to add them linearly. Back.
9 The most well-known version is that in which correlations are neglected:
Y stands for the quantity of interest, the value
of which depends
on directly measured quantities,
calibration constants and other
systematic effects (all terms generically indicated by Xi).
This formula
comes from probability theory,
but it is valid if Xi and Y are
random variables,
(Xi) are
standard deviation and the linearization is reasonable.
It is very interesting to look
at text books to see how this formula is derived.
The formula is usually initially proofed referring to random variables
associated to observables and then, suddenly, it is referred
to physics quantities, without any justification.
Back.
10 As far as ``systematic errors'' are concerned the situation is much more problematic because the ``errors'' are not even operationally well defined: they may correspond to subjectivist standard deviations (what I consider to be correct, and what corresponds to the ISO type B standard uncertainty [10]), but they can more easily be maximum deviations, ±50% variation on a selection cut, or the absolute difference obtained using two assumptions for the systematic effect. Back.
11 I am strongly convinced that a rigorous application of frequentist ideas leads nowhere. Back.
If one asks HEP physicists ``what is probability?'', one will realize immediately that they ``think they are'' frequentist. The same impression is got looking at the books and lecture notes they use [13]. Particularly significant, to get an overview of ideas and methods commonly used, are the PDG [3] and other booklets [14, 15] which have a kind of explicit (e.g. [3, 14]) or implicit (e.g. [15]) imprimatur of HEP organizations.
If, instead, one asks physicists what they think about probability as ``degree of belief'' the reaction is negative and can even be violent: ``science must be objective: there is no room for belief'', or ``I don't believe something. I assess it. This is no a matter for religion!''.
3.2. HEP physicists ``are Bayesian''
On the other hand, if one requires physicists to express their opinion about practical situations in condition of uncertainty, instead of just standard examination questions, one gets a completely different impression. One realize vividly that Science is indeed based on beliefs, very solid and well grounded beliefs, but they remain beliefs ``...in instrument types, in programs of experiment enquiry, in the trained, individual judgements about every local behavior of pieces of apparatus'' [16].
Physicists find it absolutely natural to talk about the probability of hypotheses, a concept for which there is no room in the frequentist approach. Also the intuitive way with which they figure out the result is, in fact, a probabilistic assessment on the true value. Try to ask what is the probability that the top quark mass is between 170 and 180 GeV. No one (12) will reply that the question has no sense, since ``the top quark mass is a constant of unknown value'' (as an orthodox frequentist should complain). They will simply answer that the probability is such and such percent, using the published value and ``error''. They are usually surprised if somebody tries to explain to them that they ``are not allowed'' to speak of probability of a true value.
Another word which physicists find scandalous is ``prior'' (``I don't want to be influenced by prejudices'' is the usual reply). But in reality priors play a very important role in laboratory routines, as well as at the moment of deciding that a paper is ready for publication. They allow experienced physicists to realize that something is going wrong, that a student has most probably made a serious mistake, that the result has not yet been corrected by all systematic effects, and so on. Unavoidably, priors generate some subtle cross correlations among results, and there are well known cases of the values of physics quantities slowly drifting from an initial point, with all subsequent results being included in the ``error bar'' of the previous experiment. But I think that there no one and nothing is to blame for the fact that these things happen (unless made on purpose): a strong evidence is needed before the scientific community radically changes its mind, and such evidence is often achieved after a long series of experiments. Moreover, very subtle systematic effects may affect the data, and it is not a simple task for an experimentalist to decide when all corrections have been applied, if he has no idea what the result should be.
3.3. Intuitive application of Bayes' theorem
There is an example which I like to give, in order to demonstrate that the intuitive reasoning which unconsciously transforms confidence intervals into probability intervals for the true value is, in fact, very close to the Bayes' theorem. Let us imagine we see a hunting dog in a forest and have to guess where the hunter is, knowing that there is a 50% probability that the dog is within 100 m around him. The terms of the analogy with respect to observable and true value are obvious. Everybody will answer immediately that, with 50% probability, the hunter is within 100 m from the dog. But everybody will also agree that the solution relies on some implicit assumptions: uniform prior distribution (of the hunter in the forest) and symmetric likelihood (the dog has no preferred direction, as far as we know, when he runs away from the hunter). Any variation in the assumptions leads to a different solution. And this is also easily recognized by physicists, expecially HEP physicists, who are aware of situations in which the prior is not flat (like the cases of a bremsstrahlung photon or of a cosmic ray spectrum) or the likelihood is not symmetric (not all detectors have a nice Gaussian response). In these situations intuition may still help a qualitatively guess to be made about the direction of the effect on the value of the measurand, but a formal application of the Bayesian ideas becomes crucial in order to state a result which is consistent with what can be honestly learned from data.
The fact that Bayesian inference is not currently used in HEP
does not imply
that non-trivial inverse problems remain unsolved, or that
results are usually wrong. The solution often relies on extensive
use of Monte Carlo (MC)
simulation (13)
and on intuition. The inverse problem is then
treated as a direct one. The quantities of interest are
considered as MC parameters, and
are varied until the best statistical agreement between simulation
output and experimental data is achieved. In principle, this is
a simple numerical implementation of Maximum Likelihood, but in reality
the prior distribution is also taken into account in the simulation
when it is known to be non uniform (like in the aforementioned
example of a cosmic ray experiment). So, in reality what it is often
maximized is not the likelihood, but the Bayesian posterior
(likelihood × prior), and, as said before, the result is intuitively
considered to be a probabilistic statement for the true value.
So, also in this case, the results are close to those obtainable
by Bayesian inference, especially if the
posterior is almost Gaussian (parabolic negative log-likelihood).
Problems may occur, instead, when the ``not used'' prior
is most likely not uniform, or when the posterior is
very non-Gaussian. In the latter case the difference between
mode and average of the distribution, and the evaluation of the uncertainty
from the ``
(log-likelihood)
= 1/2 rule'' can make quite a difference to the result.
12 Certainly one may find people aware of the ``sophistication'' of the frequentist approach, but these kinds of probabilistic statements are currently heard in conferences and no frequentist guru stands up to complain that the speaker is talking nonsense. Back.
13 If there is something in which HEP physicists really believe, it is Monte Carlo simulation! It plays a crucial role in all analyses, but sometimes its use as a multipurpose brute force problem solver is really unjustified and it can, from a cultural point of view, be counterproductive. For example, I have seen it applied to solve elementary problems which could be solved analytically, like ``proving'' that the variance of the sum of two random numbers is the sum of the variances. I once found a sentence at the end of the solution of a standard probability problem which I consider to be symptomatic of this brute force behaviour: ``if you don't trust logic, then you can make a little Monte Carlo...''. Back.
Besides the intuitive use of Bayesian reasoning, there are, in fact, some applications in which the Bayes' theorem is explicitly applied. This happens when frequentist methods ``do not work'', i.e. they give manifestly absurd results, or in solving more complicated problems than just inferring the value of a quantity, like, for example, the deconvolution of a spectrum (``unfolding''). Nevertheless, these methods are mostly used with a utilitarian spirit, without having really understood the meaning of subjective probability, or even remaining skeptical about it. They are used as one uses one of the many frequentist ``ad hoc-eries'' (14) , after it has been ``proved'' that they work by MC simulation (15) .
Some of the cases in which the conventional methods do not work have even induced the PDG [3] to present Bayesian methods. But, according to the PDG, a paper published this year [18] finally gives a frequentist solution to the problems, and this solution is recommended for publishing the results. Let us review the situation citing directly [18]: ``Classical confidence intervals are the traditional way in which high energy physicists report errors on results of experiments. ... In recent years, there has been considerable dissatisfaction ...for upper confidence limits... This dissatisfaction led the PDG to describe procedures for Bayesian interval construction in the troublesome cases: Poisson processes with background and Gaussian errors with a bounded physical region. ... In this paper, we...use (...) to obtain a unified set of classical confidence intervals for setting upper limits and quoting two-sided confidence intervals. ...We then obtain confidence intervals which are never unphysical or empty. Thus they remove an original motivation for the description of Bayesian intervals by the PDG.'' In fact, the 1998 issue of the Review of Particle Physics still exhibits the Bayesian approach (with the typical misconceptions that frequentists have about it), but then it suggests two papers by frequentists [6, 2] (``a balanced discussion'' [3]) to help practitioners to form their own idea on the subject, and, finally, it warmly recommends the new frequentist approach. It is easy to imagine what the reaction of the average HEP physicist will be when confronted by the authority of the PDG, unaware that ``the PDG'' which rules analysis methods is in reality constituted of no more than one or two persons who recommend a paper written by their friends (as is clear from the references and the cross acknowledgements). One should also notice that this paper claims important progress in statistics, but was in fact published in a physics journal (I wonder what the reaction of a referee of a statistics journal would have been...).
In conclusion, there is still a large gap between good sense and the dominating statistical culture. For this reason we must still be very careful in interpreting published results and in evaluating whether or not the conventional methods used lead to correct scientific conclusions ``by chance''. Some cases of misleading results will be described in the next section.
14 For example, this was exactly the attitude which I had some years ago, when I wrote a Bayesian unfolding program [17], and that of the large majority my colleagues who still use the program. Now, after having attended the 1998 Valencia Meeting on Bayesian Statistics, I have realized that this pragmatic frequentist-like use of Bayesian methods is rather common. Back.
15 I would like to point out that sometimes the conclusions derived from MC checks of Bayesian procedures may be misleading, as discussed in detail in [7]. Back.
As already discussed, confidence levels are intuitively thought
(and usually taught) as probabilities for the true values.
I must recognize that many frequentist books do insist
on the fact that the probability statement is not referred
to the true value. But then, when these books have to explain the
``real meaning'' of the result, they are forced to use ambiguous
sentences which remain stamped in the memory of the reader much more than the
frequentistically-correct twisted reasoning that they
try to explain. For example Frodesen et al.
[13]
speak about ``the faith we attach to this statement'', as if
``faith'' was not the same as degree of belief...);
Eadie et al.
[13]
introduce the argument saying that
``we want to find the range ...which contains the true value
° with probability
''
(16) ; and so on.
Similarly, significance levels are usually taken as probability of the tested hypothesis. Also this non-orthodox interpretation is stimulated by sentences like ``in statistical context, the words highly significant mean proved beyond a reasonable doubt''. It is also well known that the arbitrary translation of p-values into probability of the null hypothesis produces more severe mistakes than those concerning the use of confidence interval for uncertainty statements on true values.
Let us consider some real life examples of the misinterpretation of the two kinds just described.
5.1. Claims of new physics based on p-values
You may have heard in past years some rumors, or even official claims, of discoveries of ``New Physics'', i.e. of phenomenology which goes behind the so called Standard Model of elementary particles. Then, after some time, these announcements were systematically recognized as having been false alarms, with a consequent reduction in the credibility of the HEP community in the eyes of public opinion and tax payers (with easily imaginable long term aftermath for government support of this research). All these fake discoveries were based on considering low p-values as probability of the null hypothesis ``no new effect''. The most recent example of this kind is the so called 1997 ``HERA high Q2 events excess''. The H1 and ZEUS collaborations, analyzing data collected at the HERA very high energy electron-proton collider in Hamburg (Germany), found an excess of events (with respect to expectations) in the kinematical region corresponding to very hard interactions [19]. The ``combined significance'' (17) of the excess was of the order of 1%. Its interpretation as a hint of new physics was even suggested by official statement by the laboratory and by other agencies. For example the DESY official statement was ``...the joint distribution has a probability of less than one percent to come from Standard Model NC DIS processes'' [22] (then it implies ``it has a > 99% probability of not coming from the standard model!'' (18) ). Similarly, the Italian INFN reported that ``la probabilità che gli eventi osservati siano una fluttazione statistica è inferiore all'1%'' (then, it implies that ``with 99% probability, the events are not a statistical fluctuation, i.e. new physics''!). This is the reason why the press reported the news as ``scientists are practically sure they have found new physics''. What I found astonishing is that most of the people I talked to had real difficulty in understanding that this probability inversion is not legitimate. Only when I forced them to state their degree of belief using the logic of the coherent bet did it emerge that most of my colleagues would not even place a 1:1 bet in favour of the new discovery. Nevertheless, they were in favour of publishing the result because the loss function was absolutely unbalanced (an indirect Nobel prize against essentially nothing).
5.2. What does a lower mass bound mean?
The second example concerns confidence intervals, and it comes from new particle search. This has always been one of the main activities of HEP. New particles are postulated by theories and experimentalists look for evidence for them in experimental data. Usually, if the particle is not ``observed'' (19) one says that, although the observation does not disprove the existence of the particle, this is an indication of the fact that the particle is ``too heavy''. The result is then quantified by a ``lower bound'' at a ``95% confidence level''. Without entering into detail of how the limit is operationally defined (see, e.g., [24] and references therein, in particular [25], to have an idea of the level of complication reachable to solve a simple problem), I want to point out that also in this case the result can be misleading. Again I will give a real life example. A combined analysis of all the LEP experiments on the Higgs mass concluded recently that ``A 95% confidence level lower bound of 77.5 GeV/c2 is obtained for the mass of the Standard Model Higgs boson'' (20) . This sounds as if one were sure at 95% that the mass is above the quoted bound. In fact, most of the people I interviewed about the meaning of the statement, even those belonging to the LEP experimental teams, answered ``if the Higgs boson exists at all, then there is 95% probability that its mass is above the limit''. There were also a few people who answered ``if I do a MC simulation of the decay of a 77.5 GeV Higgs boson, I get in only 5% of the cases the simulation describing the data'', or ``if there is an Higgs boson and its mass is less than 77.5 GeV, then the observations of the search experiments have a probability of at most 5% of being correct'', or something similar. From all of which it is very difficult to understand, from a logical point of view, why one should be 95% confident that the mass is higher than the bound (21) .
The problem can be solved easily with Bayesian methods (see [7] for details). Assuming a flat prior for the mass, one finds that the value of the lower bound is more or less the published one, but only under the condition that the mass does not exceed the kinematical limit of the studied reaction. But this limit is just a few GeV above the stated lower bound. Thus in order to obtain the correct result one needs to renormalize the probability taking account of the possible range of masses above the kinematical limit and for which the experiment has no sensitivity. For this reason, in the case of [24] the probability that the mass value is above 77.5 GeV/c2 may easily become 99.9%, or more, depending on the order of magnitude of a possible upper bound for the mass. Then, in practice these lower bounds can be taken as certainties (22) .
16 I think that Aristoteles would have
gotten mad if
somebody had tried to convince him that the proposition
``the range contains
° with
probability ''
does not imply
``° is in
that range with probability
''.
Back.
17 Physicists are not familiar with the term p-value (readers not familiar with this term may find a concise review in [20]). Moreover, they are usually not aware of the implications of the fact that the statistical significance takes into account also the probability of unobserved data (see, e.g., [21]). Back.
18 One might think that the misleading meaning of that sentence was due to unfortunate wording, but this possibility is ruled out by other statements which show clearly a quite odd point of view of probabilistic matter. In fact the DESY 1998 activity report [23] insists in saying that ``the likelihood that the data produced is the result of a statistical fluctuation, ..., is equivalent to that of tossing a coin and throwing seven 'heads' or 'tails' in a row'' (replacing 'probability' by 'likelihood' does not change the sense of the message). Then, trying to explain the meaning of a statistical fluctuation, the following example is given: ``This process can be simulated with a die. If the number of times a die is thrown is sufficiently large, the die falls equally often on all faces, i.e. all six numbers occur equally often. The probability for each face is exactly a sixth or 16.66% - assuming the die is not loaded. If the die is thrown less often, then the probability curve for the distribution of the six die values is no longer a straight line but has peaks and troughs. The probability distribution obtained by throwing the die varies about the theoretical value of 16.66% depending on how many times it is thrown''. Back.
19 This concept of ``observation'' is not like that of seeing a black swan, to mention a famous classical example. New particles leave signatures in the detector that on an event by event basis cannot be distinguished by other processes (background). A statistical (inferential) analysis is therefore needed. Back.
20 In the meanwhile new data have increased this limit, but the actual number is irrelevant for this discussion. Back.
21 There was also somebody who refused to answer because ``your question is going to be difficult to answer'', or without any justification (perhaps they realized that it was impossible to explain the statement to a scientific journalist, or to a government authority - these were the terms of my question - without using probabilistic statements which were incompatible with what they thought about probability). Back.
22 There are in fact theorists who ``assume'' the lower bounds as certain bounds in their considerations. Perhaps they do it intuitively, or because they have heard in the last decades of thousands of these 95% lower bounds, and never a particle has then shown up in the 5% side... Back.
2 fit
I consider myself to be using a Bayesian method,
although in a simplified form. This attitude contrasts
to that of practitioners who use methods in which the Bayes' theorem
is explicitly applied, but as if it were one of the many
frequentist cooking recipes.
Finally, I would like to give a last recommendation. Don't try to convince a physicist that he already is Bayesian, or that you want to convert him to become Bayesian. A physicist feels offended if you call him ``X-ian'', be it Newtonian, Fermian, or Einsteinian. But, being human, he has a natural feel for probability, just like everybody else. I would like to generalize this idea and propose reducing the use of the adjective ``Bayesian''. I think that the important thing is to have a theory of uncertainty in which ``probability'' has the same meaning for everybody, precisely that meaning which the human mind has naturally developed and that frequentists have tried to kill. Therefore I would rather call these methods probabilistic methods. And I conclude saying that, obviously, ``I am not a Bayesian''.
It is a pleasure to thank the organizers of Maxent98 for the warm hospitality in Garching, which favoured friendly and fruitful discussions among the participants.
23 For example frequentists completely misunderstand this points, when they state, e.g., that ``Bayesian methods proceed by invoking an interpretation of Bayes' theorem, in which one deems it sensible to consider a p.d.f. for the unknown true value mt'', or that ``a pragmatist can consider the utility of equations generated by the two approaches while skirting the issue of buying a whole philosophy of science' [6].
I find that also the Zellner's paper [26] demonstrating that Bayes' theorem makes the best use of the available information can help a lot to convince people. Back.
24 Although it may seem absurd, the Bayesian approach is recognized by ``frequentists'' to be ``well adapted to decision-making situations'' [3] (see also [6, 18]). I wonder what then probability is for these authors. Back.
25 Dogmatism is never desirable. It can be easily turned against the theory. For example, one criticism of [18] says, more or less, that Bayesian theory supports Jeffreys' priors, and not uniform priors, but, since Jeffreys' priors give unreasonable results in their application, then one should mistrust Bayesian methods! (see also [28].) One may object that the meaning and the role of Jeffreys' priors was misunderstood, but it seems to me difficult to control the use of objective priors or of reference analysis once they have left the community of experts aware of the ``rather special nature and role of the concept of a `minimally informative' prior specification - appropriately defined!'' [29]. Back.