*I’m reblogging a few of the Higgs posts, with some updated remarks, on this two-year anniversary of the discovery. (The first was in my last post.) The following, was originally “Higgs Analysis and Statistical Flukes: part 2″ (from March, 2013**).[1]*

Some people say to me: “This kind of reasoning is fine for a ‘sexy science’ like high energy physics (HEP)”–as if their statistical inferences are radically different. But I maintain that this is the mode by which data are used in “uncertain” reasoning across the entire landscape of science and day-to-day learning (at least, when we’re trying to find things out)[2] Even with high level theories, the particular problems of learning from data are tackled piecemeal, in local inferences that afford error control. Granted, this statistical philosophy differs importantly from those that view the task as assigning comparative (or absolute) degrees-of-support/belief/plausibility to propositions, models, or theories.

**“Higgs Analysis and Statistical Flukes: part 2”**

Everyone was excited when the Higgs boson results were reported on July 4, 2012 indicating evidence for a Higgs-like particle based on a “5 sigma observed effect”. The observed effect refers to the number of *excess events* of a given type that are “observed” in comparison to the number (or proportion) that would be expected from background alone, and not due to a Higgs particle. This continues my earlier post (part 1). It is an outsider’s angle on one small aspect of the statistical inferences involved. But that, apart from being fascinated by it, is precisely why I have chosen to discuss it: we [philosophers of statistics] should be able to employ a general philosophy of inference to get an understanding of what is true about the controversial concepts we purport to illuminate, e.g., significance levels.

Here I keep close to an official report from ATLAS, researchers define a “global signal strength” parameter “such that μ = 0 corresponds to the background only hypothesis and μ = 1 corresponds to the SM Higgs boson signal in addition to the background” (where SM is the Standard Model). The statistical test may be framed as a one-sided test, where the test statistic (which is actually a ratio) records differences in the positive direction, in standard deviation (sigma) units. Reports such as

Pr(Test T would yield at least a 5 sigma excess;

H_{0}: background only) = extremely low

are deduced from the sampling distribution of the test statistic, fortified with much cross-checking of results (e.g., by modeling and simulating relative frequencies of observed excesses generated with “Higgs signal +background” compared to background alone). The inferences, even the formal statistical ones, go beyond p-value reports. For instance, they involve setting lower and upper bounds such that values excluded are ruled out with high severity, to use my term. But the popular report is in terms of the observed 5 sigma excess in an overall test T, and that is mainly what I want to consider here.

*Error probabilities*

In a Neyman-Pearson setting, a cut-off c_{α}_{ }is chosen pre-data so that the probability of a type I error is low. In general,

Pr(

d(X) > c_{α};H_{0}) ≤ α

and in particular,alluding to an overall test T:

(1) Pr(Test T yields

d(X) > 5 standard deviations;H_{0}) ≤ .0000003.

The test at the same time is designed to ensure a reasonably high probability of detecting global strength discrepancies of interest. (I always use “discrepancy” to refer to parameter magnitudes, to avoid confusion with observed differences).

[Notice these are not likelihoods.] Alternatively, researchers can report observed standard deviations (here, the sigmas), or equivalently, the associated observed statistical significance probability, *p*_{0}. In general,

Pr(

P<p_{0};H_{0}) <p_{0}

and in particular,

(2) Pr(Test T yields

P<.0000003;H_{0}) < .0000003.

For test T to yield a “worse fit” with *H*_{0 }(smaller p-value) due to background alone is sometimes called “a statistical fluke” or a “random fluke”, and the probability of so statistically significant a random fluke is ~0. With the March 2013 results, the 5 sigma difference has grown to 7 sigmas.

So probabilistic statements along the lines of (1) and (2) are standard.They allude to sampling distributions, either of test statistic *d*(**X)**, or the P-value viewed as a random variable. They are scarcely illicit or prohibited. (I return to this in the last section of this post).

*An implicit principle of inference or evidence*

Admittedly, the move to taking the 5 sigma effect as evidence for a genuine effect (of the Higgs-like sort) results from an implicit principle of evidence that I have been calling the severity principle (SEV). Perhaps the weakest form is to a statistical rejection or falsification of the null. (I will deliberately use a few different variations on statements that can be made.)

Datax_{0 }from a test T provide evidence for rejecting H_{0}(just) to the extent that H_{0}would (very probably) have survived, were it a reasonably adequate description of the process generating the data (with respect to the question).

It is also captured by a general frequentist principle of evidence (FEV) (Mayo and Cox 2010), a variant on the general idea of severity (SEV) (EGEK 1996, Mayo and Spanos 2006, etc.).

The sampling distribution is computed, under the assumption that the production of observed results is similar to the “background alone”, with respect to relative frequencies of signal-like events. (Likewise for computations under hypothesized discrepancies.) The relationship between *H*_{0}* *and the probabilities of outcomes is an intimate one: the various statistical nulls live their lives to refer to aspects of general types of data generating procedures (for a taxonomy, see Cox 1958, 1977). “*H** _{0 }*is true” is a shorthand for a very long statement that

*H*

*is an approximately adequate model of a specified aspect of*

_{0}*the process generating the data in the context. (This relates to statistical models and hypotheses living “lives of their own”.)*

*Severity and the detachment of inferences*

The sampling distributions serve to give counterfactuals. In this case they tell us what it would be like, statistically, were the mechanism generating the observed signals similar to *H*_{0}.[i] While one would want to go on to consider the probability test T yields so statistically significant an excess under various alternatives to μ = 0, this suffices for the present discussion. Sampling distributions can be used to arrive at error probabilities that are relevant for understanding the capabilities of the test process, in relation to something we want to find out..*Since a relevant test statistic is a function of the data and quantities about which we want to learn, the associated sampling distribution is the key to inference*. (This is why bootstrap, and other types of, resampling works when one has a random sample from the process or population of interest.)

The *severity principle*, put more generally:

Data from a test T[ii]provide good evidence for inferring H (just) to the extent that H passes severely withx_{0}, i.e., to the extent that H would (very probably) not have survived the test so well were H false.

(The severity principle can also be made out just in terms of relative frequencies, as with bootstrap re-sampling.)* *In this case, what is surviving is minimally the non-null. Regardless of the specification of a statistical inference, to assess the severity associated with a claim H requires considering H’s denial: together they exhaust the answers to a given question.

Without making such a principle explicit, some critics assume the argument is all about the reported p-value. The inference actually **detached** from the evidence can be put in any number of ways, and no uniformity is to be expected or needed:

(3) There is strong evidence for H: a Higgs (or a Higgs-like) particle.

(3)’ They have experimentally demonstrated H: a Higgs (or Higgs-like) particle.

Or just, infer H.

Doubtless particle physicists would qualify these statements, but nothing turns on that. ((3) and (3)’ are a bit stronger than merely falsifying the null because certain properties of the particle must be shown. I leave this to one side.)

As always, the mere p-value is a pale reflection of the detailed information about the consistency of results that really fortifies the knowledge of a genuine effect. Nor is the precise improbability level what matters. We care about the inferences to real effects (and estimated discrepancies) that are warranted.

*Qualifying claims by how well they have been probed*

The inference is qualified by the statistical properties of the test, as in (1) and (2), but that does not prevent detaching (3). This much is shown: they are able to experimentally demonstrate the Higgs particle. They can take that much of the problem as solved and move on to other problems of discerning the properties of the particle, and much else that goes beyond our discussion*. There is obeisance to the strict fallibility of every empirical claim, but there is no probability assigned. Neither is there in day-to-day reasoning, nor in the bulk of scientific inferences, which are not formally statistical. Having inferred (3), granted, one may say informally, “so probably we have experimentally demonstrated the Higgs”, or “probably, the Higgs exists” (?). Or an informal use of “likely” might arise. But whatever these might mean in informal parlance, they are not formal mathematical probabilities. (As often argued on this blog, discussions on statistical philosophy must not confuse these.)

[We can however write, SEV(H) ~1]

The claim in (3) is approximate and limited–as are the vast majority of claims of empirical knowledge and inference–and, moreover, we can say in just what ways. It is recognized that subsequent data will add precision to the magnitudes estimated, and may eventually lead to new and even entirely revised interpretations of the known experimental effects, models and estimates. That is what cumulative knowledge is about. (I sometimes hear people assert, without argument, that modeled quantities, or parameters, used to describe data generating processes are “things in themselves” and are outside the realm of empirical inquiry. This is silly. Else we’d be reduced to knowing only tautologies and maybe isolated instances as to how “I seem to feel now,” attained through introspection.)

*Telling what’s true about significance levels*

So we grant the critic that something like the severity principle is needed to move from statistical information plus background (theoretical and empirical) to inferences about evidence and inference (and to what levels of approximation). It may be called lots of other things and framed in different ways, and the reader is free to experiment . What we should not grant the critic is any allegation that there should be, or invariably is, a link from a small observed significance level to a small posterior probability assignment to *H** _{0}*. Worse, (1- the p-value) is sometimes alleged to be the posterior probability accorded to the Standard Model itself! This is neither licensed nor wanted!

If critics (or the p-value police, as Wasserman called them) maintain that Higgs researchers are misinterpreting their significance levels, correct them with the probabilities in (1) and (2). If they say, it is patently obvious that Higgs researchers want to use the p-value as a posterior probability assignment to *H** _{0}*, point out the more relevant and actually attainable [iii] inference that is detached in (3). If they persist that what is really, really wanted is a posterior probability assignment to the inference about the Higgs in (3), ask why? As a formal posterior probability it would require a prior probability on all hypotheses that could explain the data. That would include not just

*H*and

*H*

_{0}**but all rivals to the Standard Model, rivals to the data and statistical models, and higher level theories as well. But can’t we just imagine a Bayesian catchall hypothesis? On paper, maybe, but where will we get these probabilities? What do any of them mean? How can the probabilities even be comparable in different data analyses, using different catchalls and different priors?[iv]**

Degrees of belief will not do. Many scientists perhaps had (and have) strong beliefs in the Standard Model before the big collider experiments—given its perfect predictive success. Others may believe (and fervently wish) that it will break down somewhere (showing supersymmetry or whatnot); a major goal of inquiry is learning about viable rivals and how they may be triggered and probed. Research requires an open world not a closed one with all possibilities trotted out and weighed by current beliefs. [v] We need to point up what has not yet been well probed which, by the way, is very different from saying of a theory that it is “not yet probable”.

*Those prohibited phrases*

One may wish to return to some of the condemned phrases of particular physics reports.Take,

“There is less than a one in a million chance that their results are a statistical fluke”.

This is not to assign a probability to the null, just one of many ways (perhaps not the best) of putting claims about the sampling distribution: The statistical null asserts that Ho: background alone adequately describes the process.

Ho does not assert the results are a statistical fluke, but it tells us what we need to determine the probability of observed results “under Ho”. In particular, consider all outcomes in the sample space that are further from the null prediction than the observed, in terms of p-values {x: p < po}. Even when Ho is true, such “signal like” outcomes may occur. They are po level flukes. Were such flukes generated even with moderate frequency under Ho, they would not be evidence against Ho. But in this case, such flukes occur a teeny tiny proportion of the time. Then SEV enters: if we are regularly able to generate such teeny tiny p-values, we have evidence of a genuine discrepancy from Ho.

I am repeating myself, I realize, on the hopes that at least one phrasing will drive the point home. Nor is it even the improbability that substantiates this, it is the fact that an extraordinary set of coincidences would have to have occurred again and again. To nevertheless retain Ho as the source of the data would block learning. (Moreover, they know that if some horrible systematic mistake was made, it would be detected in later data analyses.)

I will not deny that there have been misinterpretations of p-values, but if a researcher has just described performing a statistical significance test, it would be “ungenerous” to twist probabilistic assertions into posterior probabilities. It would be a kind of “confirmation bias” whereby one insists on finding one sentence among very many that could conceivably be misinterpreted Bayesianly.

*Triggering, indicating, inferring*

As always, the error statistical philosopher would distinguish different questions at multiple stages of the inquiry. The aim of many preliminary steps is “behavioristic” and performance oriented: the goal being to control error rates on the way toward finding excess events or bumps of interest.

I hope it is (more or less) clear that burgandy is new; black is old. If interested: *See statistical flukes (part 3)*

The original posts of parts 1 and 2 had around 30 comments each; you might want to look at them:

Part 1: http://errorstatistics.com/2013/03/17/update-on-higgs-data-analysis-statistical-flukes-1/

Part 2 http://errorstatistics.com/2013/03/27/higgs-analysis-and-statistical-flukes-part-2/

*Fisher insisted that to assert a phenomenon is experimentally demonstrable:[W]e need, not an isolated record, but a reliable method of procedure. In relation to the test of significance, we may say that a phenomenon is experimentally demonstrable when we know how to conduct an experiment which will rarely fail to give us a statistically significant result. (Fisher Design of Experiments 1947, 14).

New Notes

[1] I plan to do some new work in this arena soon, so I’ll be glad to have comments.

[2] I have often noted that there are other times where we are trying to find evidence to support a previously held position.

REFERENCES (from March, 2013 post):

ATLAS Collaboration (November 14, 2012), Atlas Note: “Updated ATLAS results on the signal strength of the Higgs-like boson for decays into WW and heavy fermion final states”, ATLAS-CONF-2012-162. http://cds.cern.ch/record/1494183/files/ATLAS-CONF-2012-162.pdf

Cox, D.R. (1958), “Some Problems Connected with Statistical Inference,” *Annals of Mathematical Statistics*, 29: 357–72.

Cox, D.R. (1977), “The Role of Significance Tests (with Discussion),” *Scandinavian Journal of Statistics*, 4: 49–70.

Mayo, D.G. (1996), *Error and the Growth of Experimental Knowledge*, University of Chicago Press, Chicago.

Mayo, D. G. and Cox, D. R. (2010). “Frequentist Statistics as a Theory of Inductive Inference” in *Error and Inference: Recent Exchanges on Experimental Reasoning, Reliability and the Objectivity and Rationality of Science* (D Mayo and A. Spanos eds.), Cambridge: Cambridge University Press: 247-275.

Mayo, D.G., and Spanos, A. (2006), “Severe Testing as a Basic Concept in a Neyman-Pearson Philosophy of Induction,” *British Journal of Philosophy *of *Science*, 57: 323–357.

___________

Original notes:

[i] This is a bit stronger than merely falsifying the null here, because certain features of the particle discerned must also be shown. I leave details to one side.

[ii] Which almost always refers to a set of tests, not just one.

[iii] I sense that some Bayesians imagine P(H) is more “hedged” than to actually infer (3). But the relevant hedging, the type we can actually attain, is given by an assessment of severity or corroboration or the like. Background enters via a repertoire of information about experimental designs, data analytic techniques, mistakes and flaws to be wary of, and a host of theories and indications about which aspects have/have not been severely probed. Many background claims enter to substantiate the error probabilities; others do not alter them.

[iv]In aspects of the modeling, researchers make use of known relative frequencies of events (e.g., rates of types of collisions) that lead to legitimate, empirically based, frequentist “priors” if one wants to call them that.

[v] After sending out the letter, prompted by Lindley, O’Hagan wrote up a synthesis http://errorstatistics.com/2012/08/25/did-higgs-physicists-miss-an-opportunity-by-not-consulting-more-with-statisticians/

I apologize if this has already been covered, and also must apologize for not having read the details of exactly how the Higgs people did their experiments and analysis. I wish I had more time to follow this issue closely. But allow me to raise a question anyway.

Putting aside from the interesting issues of whether the physicists really meant their p-values to be posterior probabilities, or that some people took them as such, what about model bias? Wouldn’t model bias potentially give a 5-sigma result, even if H0 is true? If so, Larry’s “P-values generally can be misleading, but we should make an exception in this momentous situation” statement (I’m paraphrasing here) cannot be valid.

In addition to model bias along the lines of something like not accounting for problems in the measuring hardware, there is the issue of assuming a normal distribution. There is no such thing as an exact normal distribution in nature, and though it is an adequate model in tons of contexts, using this model so far out in the tails is extremely questionable.

Matt: This is a fairly extensive modeling enterprise where knowledge of background effects is extremely extensive. I don’t agree with the quoted sentence from Wasserman. (Is that from his post?) He mounted an excellent defense of the sophistication of statistics among HEPP on the ISBA site (link on last post). I will be discussing some of the details of cousin’s paper: Here’s a link to his recent paper on the Higgs and foundations of statistics http://arxiv.org/abs/1310.3791)..

It’s worth mentioning that particle physicists have a convention of reporting results in z-scores and sigmas, but these are backed out of the p-value calculations and do not necessarily imply a normal model or normal approximation.

Corey: “back out of the p-value”? I don’t know what you mean. Also, the Higgs 5 sigma computation is based on Normal distributions.

“If one observes data that disagree with the null hypothesis, that is data having a small probability of being observed if the null hypothesis is tue, one may convert that probability into the corresponding number of “sigma”, i.e. standard deviations units, from a Gaussian mean. A 16% probability is a one-standard-deviation effect; a 0.17% probability is a three-standard-deviation effect; and a 0.000027% probability corresponds to five standard deviations – “five sigma” for insiders.” — Tommaso Dorigo

That is, you can get a p-value from any appropriate calculation and then compute the z-score that corresponds to that p-value using the normal CDF.

Corey:Yes,the P-values correspond to z-scores–e.g., “A 16% probability is a one-standard-deviation effect”. So?

Particle physics has a tradition of seeking 5-sigma even if the model that leads to the p-value in question is not the normal distribution. By convention the results are phrased in terms of how many sigma have been achieved, but this should not be taken to indicate that a normal model was used to compute the p-value.

All of this is in response to Norm Matloff’s, “There is no such thing as an exact normal distribution in nature, and though it is an adequate model in tons of contexts, using this model so far out in the tails is extremely questionable.”

Now I’m really confused. Was a normal model used in the Higgs analysis or not? Was the p-value 0.000027% or not? Was the test statistic 5 standard deviations away (from something) or not? You seem to be saying that the answer to the last question (and the first) is “not necessarily,” i.e. that there actually was no real sigma involved. If that is the case, such misrepresentation, or at the least, such sloppy thinking, isn’t inspiring confidence in their findings, on my part.

Did you ever sort this out? It appears from the Cousins paper you linked to (section 5.2) that there is a long-tradition in high-energy physics of doing exactly what Corey described. A lot of work is put into estimating the distribution of a likelihood ratio statistic under the null, the observed likelihood then gives a p-value in this distribution (there is no assumption of normality), and a normal-distribution equivalent in sigmas is then backed out and reported.

As I said, I was paraphrasing Larry’s remarks. His actual statement (yes, from the post you linked to in your Part 1) was “The whole enterprise of hypothesis testing is overused. But, there are times when it is just the right tool and the search for the Higgs is a perfect example.” His point apparently was that though p-values can be misleading because they can pounce on a tiny but uninteresting departure from H0, there are some situations in which ANY departure is important. My response is that a “departure” may be purely due to model bias.

I look forward to reading your remarks on the Cousins paper.

Matt: Yes, that makes more sense (about Larry). The HEP people work very hard to triangulate and simulate their uses of models by really getting to know how it behaves with background alone. Of course, I’m an outsider.

Matloff: I don’t know about the details in this particular case either, but generally the answer is: It depends. Optimally one would like to have an upper bound on the p-value over a “full neighbourhood” of the nominal H0, i.e., all kinds of distributions that are not exactly normal but would still be “interpretatively equivalent”. Such an analysis is hardly ever done formally (although robust statisticians have results of this kind in specific setups). However, looking at the data in specific situations it is indeed often pretty clear that what was observed is not only incompatible with the nominal H0, but with everything that could be seen as “interpretatively equal”. If your H0 is i.i.d. N(0,sigma^2) (but anything about symmetric and unimodal with an about zero center is “interpretationally equivalent”), and more than 900 out of thousand observations are larger than “about zero”, that should be clear enough. I agree though that this cannot be seen from discussing the p-value alone.

I think some commentators may be downplaying the main point of my (3): severity and the detachment of inferences–put the emphasis on “detachment”. Putting together strong arguments from coincidence or severe tests enable ampliative inferences–they go beyond the data–there’s lift-off– but they are qualified and based on the error properties of the overall procedure. That’s inductive learning, at least on the statistical philosophy I favor.