S. Senn: “Responder despondency: myths of personalized medicine” (Guest Post)

Stephen Senn

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Stephen Senn
Head, Methodology and Statistics Group
Competence Center for Methodology and Statistics (CCMS)
Luxembourg

Responder despondency: myths of personalized medicine

The road to drug development destruction is paved with good intentions. The 2013 FDA report, Paving the Way for Personalized Medicine  has an encouraging and enthusiastic foreword from Commissioner Hamburg and plenty of extremely interesting examples stretching back decades. Given what the report shows can be achieved on occasion, given the enthusiasm of the FDA and its commissioner, given the amazing progress in genetics emerging from the labs, a golden future of personalized medicine surely awaits us. It would be churlish to spoil the party by sounding a note of caution but I have never shirked being churlish and that is exactly what I am going to do.

Reading the report, alarm bells began to ring when I came across this chart (p17) describing the percentage of patients for whom drug are ineffective. Actually, I tell a lie. The alarm bells were ringing as soon as I saw the title but by the time I saw this chart, the cacophony was deafening.

senn responder pic

The question that immediately arose in my mind was ‘how do the FDA know this is true?’ Well, the Agency very helpfully tells you how they know this is true. They cite a publication, ‘Clinical application of pharmacogenetics’[1] as the source of the chart. Slightly surprisingly, the date of the publication predates the FDA report by 12 years (this is pre-history in pharmacogenetic terms) however, sure enough, if you look up the cited paper you will find that the authors (Spear et al) state ‘We have analyzed the efficacy of major drugs in several important diseases based on published data, and the summary of the information is given in Table 1.’ This is Table 1:

senn responder table 1

Now, there are a few differences here to the FDA report but we have to give the Agency some credit. First of all they have decided to concentrate on those who don’t respond, so they have subtracted the response rates from 100. Second, they have obviously learned an important data presentation lesson: sorting by the alphabet is often inferior to sorting by importance. Unfortunately, they have ignored an important lesson that texts on graphical excellence impart: don’t clutter your presentation with chart junk[2]. However, in the words of Meatloaf, ‘Two out of three ain’t bad,’ so I have to give them some credit.

However, that’s not quite the end of the story. Note the superscripted 1 in the rubric of the source for the FDA claim. That’s rather important. This gives you the source of the information, which is the Physician’s Desk Reference, 54th edition, 2000.

At this point of tracing back, I discovered what I knew already. What the FDA is quoting are zombie statistics. This is not to impugn the work of Spear et al. The paper makes interesting points. (I can’t even blame them for not citing one of my favourite papers[3], since it appeared in the same year.) They may well have worked diligently to collect the data they did but the trail runs cold here. The methodology is not given and the results can’t be checked. It may be true, it may be false but nobody, and that includes the FDA and its commissioner, knows.

But there is a further problem. There is a very obvious trap in using observed response rates to judge what percentage of patient respond (or don’t). That is that all such measures are subject to within-patient variability. To take a field I have worked in, asthma, if you take (as the FDA has on occasion) 15% increase in Forced Expiratory Volume in one second (FEV1) above baseline as indicating a response. You will classify someone with a 14% value as a non-responder and someone with a 16 % value as a responder but measure them again and they could easily change places (see chapter 8 of Statistical Issues in Drug Development[4]) . For a bronchodilator I worked on, mean bronchodilation at 12 hours was about 18% so you simply needed to base your measurement of effect on a number of replicates if you wanted to increase the proportion of responders.

There is a very obvious trap (or at least it ought to be obvious to all statisticians) in naively using reported response rates as an indicator of variation in true response[5]. This can be illustrated using the graph below. On the left hand side you see an ideal counterfactual experiment. Every patient can be treated under identical conditions with both treatments. In this thought experiment the difference that the treatment makes to each patient is constant. However, life does not afford us this possibility. If what we choose to do is run a parallel group trial we will have to randomly give the patient either placebo or the active treatment. The right hand panel shows us what we will see and is obtained by randomly erasing one of the two points for each patient on the left hand panel. It is now impossible to judge individual response: all that we can judge is the average.

senn responder graphs

Of course, I fixed things in the example so that response was constant and it clearly might not be. But that is not the point. The point is that the diagram shows that by naively using raw outcomes we will overestimate the personal element of response. In fact, only repeated cross-over trial can reliable tease out individual response from other components of variation and in many indications these are not possible and even where they are possible they are rarely run[6].

So to sum up, the reason the FDA ‘knows’ that 40% of asthmatic patients don’t respond to treatment is because a paper from 2001, with unspecified methodology, most probably failing to account for within patient variability, reports that the authors found this to be the case by studying the Physician’s Desk Reference.

This is nothing short of a scandal. I don’t blame the FDA. I blame me and my fellow statisticians. Why and how are we allowing our life scientist colleagues to get away with this nonsense? They genuinely believe it. We ought to know better.

References

  1. Spear, B.B., M. Heath-Chiozzi, and J. Huff, Clinical application of pharmacogenetics. Trends in Molecular Medicine, 2001. 7(5): p. 201-204.
  2. Tufte, E.R., The Visual Display of Quantitative Information. 1983, Cheshire Connecticut: Graphics Press.
  3. Senn, S.J., Individual Therapy: New Dawn or False Dawn. Drug Information Journal, 2001. 35(4): p. 1479-1494.
  4. Senn, S.J., Statistical Issues in Drug Development. 2007, Hoboken: Wiley. 498.
  5. Senn, S., Individual response to treatment: is it a valid assumption? BMJ, 2004. 329(7472): p. 966-8.
  6. Senn, S.J., Three things every medical writer should know about statistics. The Write Stuff, 2009. 18(3): p. 159-162.

 

Categories: evidence-based policy, Statistics, Stephen Senn | 25 Comments

Continued:”P-values overstate the evidence against the null”: legit or fallacious?

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continued…

2. J. Berger and Sellke and Casella and R. Berger

Of course it is well-known that for a fixed P-value, with a sufficiently large n, even a statistically significant result can correspond to large posteriors in H0 (Jeffreys-Good-Lindley paradox).  I.J. Good (I don’t know if he was the first) recommended decreasing the required P-value as n increases, and had a formula for it. A more satisfactory route is to ensure the interpretation takes account of the (obvious) fact that with a fixed P-value and increasing n, the test is more and more sensitive to discrepancies–much as is done with lower/upper bounds of confidence intervals. For some rules of thumb see Section 5.

The JGL result is generalized in J. Berger and Sellke (1987). They make out the conflict between P-values and Bayesian posteriors by considering the two sided test of the Normal mean, H0: μ = μ0 versus H1: μ ≠ μ0 .

“If n = 50…, one can classically ‘reject H0 at significance level p = .05,’ although Pr (H0|x) = .52 (which would actually indicate that the evidence favors H0).” (Berger and Sellke, 1987, p. 113).

If n = 1000, a result statistically significant at the .05 level leads to a posterior to the null going from .5 to .82!

While from their Bayesian perspective, this appears to supply grounds for denying P-values are adequate for assessing evidence, significance testers rightly balk at the fact that using the recommended priors allows highly significant results to be interpreted as no evidence against the null–or even evidence for it!

From J. Berger and T. Selke (1987) “Testing a Point Null Hypothesis,” JASA 82(397) : 113.

Many think this shows that the P-value ‘overstates evidence against a null’ because it claims to use an ‘impartial’ Bayesian prior probability assignment of .5 to H0, the remaining .5 spread out over the alternative parameter space. (But see the justification Berger and Sellke give in Section 3. A Dialogue.) Casella and R. Berger (1987) charge that the problem is not P-values but the high prior, and that “concentrating mass on the point null hypothesis is biasing the prior in favor of Has much as possible” (p. 111) whether in 1 or 2-sided tests. Note, too, the conflict with confidence interval reasoning since the null value (here it is 0) lies outside the corresponding confidence interval (Mayo 2005). See Senn’s very interesting points on this same issue in his letter (to Goodman) here.

^^^^^^^^^^^^^^^^^

3. A Dialogue (ending with a little curiosity in J. Berger and Sellke):

So a guy is fishing in Lake Elba, and a representative from the EPA (Elba Protection Association) points to notices that mean toxin levels in fish were found to exceed the permissible mean concentration, set at 0.

EPA Rep: We’ve conducted two studies (each with random sample of 100 fish) showing statistically significant concentrations of toxin, at low P-values, e.g., .02. 

P-Value denier: I deny you’ve shown evidence of high mean toxin levels; P-values exaggerate the evidence against the null.

EPA Rep: Why is that?

P-value denier: If I update the prior of .5 that I give to the null hypothesis (asserting toxin levels are of no concern), my posterior for H0 is still not all that low, not as low as .05 for sure.

EPA Rep: Why do you assign such a high prior probability to H0?

P-value denier: If I gave H0 a value lower than .5, then, if there’s evidence to reject H0 , at most I would be claiming an improbable hypothesis has become more improbable. Who would be convinced by the statement ‘I conducted a Bayesian test of H0, assigning prior probability .1 to H0, and my conclusion is that Hhas posterior probability .05 and should be rejected’?

The last sentence is a direct quote from Berger and Sellke!

There’s something curious in assigning a high prior to the null H0–thereby making it harder to reject (or find evidence against) H0–and then justifying the assignment by saying it ensures that, if you do reject H0, there will be a meaningful drop in the probability of H0. What do you think of this?

^^^^^^^^^^^^^^^^^^^^

4. The real puzzle.

I agree with J. Berger and Sellke that we should not “force agreement”. What’s puzzling to me is why it would be thought that an account that manages to evaluate how well or poorly tested hypotheses are–as significance tests can do–would want to measure up to an account that can only give a comparative assessment (be they likelihoods, odds ratios, or other) [ii]. From the perspective of the significance tester, the disagreements between (audited) P-values and posterior probabilities are an indictment, not of the P-value, but of the posterior, as well as the Bayes ratio leading to the disagreement (as even one or two Bayesians appear to be coming around to realize, e.g., Bernardo 2011, 58-9). Casella and R. Berger show that for sensible priors with one-sided tests, the P-value can be “reconciled” with the posterior, thereby giving an excellent retort to J. Berger and Sellke. Personally, I don’t see why an error statistician would wish to construe the P-value as how “believe worthy” or “bet worthy” statistical hypotheses are. Changing the interpretation may satisfy J. Berger’s call for “an agreement on numbers” (and never mind philosophies), but doing so precludes the proper functioning of P-values, confidence levels, and other error probabilities. And “what is the intended interpretation of the prior, again?” you might ask. Aside from the subjective construals (of betting and belief, or the like), the main one on offer (from the conventionalist Bayesians) is that the prior is undefined and is simply a way to compute a posterior. Never mind that they don’t agree on which to use. Your question should be: “Please tell me: how does a posterior, based on an undefined prior used solely to compute a posterior, become “the” measure of evidence that we should aim to match?” 

^^^^^^^^^^^^^^^^

5. (Crude) Benchmarks for taking into account sample size:

Throwing out a few numbers may give sufficient warning to those inclined to misinterpret statistically significant differences at a given level but with varying sample sizes (please also search this blog [iii]). Using the familiar example of Normal testing with T+ :

H0: μ ≤ 0 vs. H1: μ > 0.  

Let σ = 1, n = 25, so σx= (σ/√n).

For this exercise, fix the sample mean M to be just significant at the .025 level for a 1-sided test, and vary the sample size n. In one case, n = 100, in a second, n = 1600. So, for simplicity, using the 2-standard deviation cut-off:

m0 = 0 + 2(σ/√n).

With stat sig results from test T+, we worry about unwarranted inferences of form:  μ > 0 + γ.

Some benchmarks:

 * The lower bound of a 50% confidence interval is 2(σ/√n). So there’s quite lousy evidence that μ > 2(σ/√n) (the associated severity is .5).

 *The lower bound of the 93% confidence interval is .5(σ/√n). So there’s decent evidence that μ > .5(σ/√n) (The associated severity is .93).

 *For n = 100, σ/√n = .1 (σ= 1); for n = 1600, σ/√n = .025

 *Therefore, a .025 stat sig result is fairly good evidence that μ > .05, when n = 100; whereas, a .025 stat sig result is quite lousy evidence that μ > .05, when n = 1600.

You’re picking up smaller and smaller discrepancies as n increases, when P is kept fixed. Taking the indicated discrepancy into account avoids erroneous construals and scotches any “paradox”.

^^^^^^^^^^

6. “The Jeffreys-Lindley Paradox and Discovery Criteria in High Energy Physics” (Cousins, 2014)

Robert Cousins, a HEP physicist willing to talk to philosophers and from whom I am learning about statistics in the Higgs discovery, illuminates the key issues, models and problems in his paper with that title. (The reference to Bernardo 2011 that I had in mind in Section 4 is cited on p. 26 of Cousins 2014).

^^^^^^^^^^^^^^^^^^^^^^^^^^

7. July 20, 2014: There is a distinct issue here….That “P-values overstate the evidence against the null” is often stated as an uncontroversial “given”. In calling it a “fallacy”, I was being provocative. However, in dubbing it a fallacy, some people assumed I was referring to one or another well-known fallacies, leading them to guess I was referring to the fallacy of confusing P(E|H) with P(H|E)—what some call the “prosecutor’s fallacy”. I wasn’t. Nor are Berger and Sellke committing a simple blunder of transposing conditionals. If they were, Casella and Berger would scarcely have needed to write their reply to point this out. So how shall we state the basis for the familiar criticism that P-values overstate evidence against (a null)?  I take it that the criticism goes something like this:

The problem with using a P-value to assess evidence against a given null hypothesis H0 is that it tends to be smaller, even much smaller, than an apparently plausible posterior assessment of H0, given data x (especially as n increases).  The mismatch is avoided with a suitably tiny P-value, and that’s why many recommend this tactic. [iv] Yet I say the correct answer to the question in my (new) title is: “fallacious”. It’s one of those criticisms that have not been thought through carefully, but rather repeated based on some well-known articles.

[i] We assume the P-values are “audited”, that they are not merely “nominal”, but are “actual” P-values. Selection effects, cherry-picking and other biases would alter the error probing capacity of the tests, and thus the purported P-value would fail the audit.

[ii] Note too that the comparative assessment will vary depending on the “catchall”.

[iii] See for example:

Section 6.1 “fallacies of rejection“.
Slide #8 of Spanos lecture in our seminar Phil 6334.

 [iv] So we can also put aside for the moment the issue of P-values not being conditional probabilities to begin with. We can also (I hope) distinguish another related issue, which requires a distinct post: using ratios of frequentist error probabilities, e.g., type 1 errors and power, to form a kind of “likelihood ratio” in a screening computation.

 

References (minimalist) A number of additional links are given in comments to my previous post

Berger, J. O. and Sellke, T.  (1987). “Testing a point null hypothesis: The irreconcilability of p values and evidence,” (with discussion). J. Amer. Statist. Assoc. 82: 112–139.

Cassella G. and Berger, R..  (1987). “Reconciling Bayesian and Frequentist Evidence in the One-sided Testing Problem,” (with discussion). J. Amer. Statist. Assoc. 82 106–111, 123–139.

Blog posts:

Comedy Hour at the Bayesian Retreat: P-values versus Posteriors.
Highly probable vs highly probed: Bayesian/ error statistical differences.

 

Categories: Bayesian/frequentist, CIs and tests, fallacy of rejection, highly probable vs highly probed, P-values, Statistics | 35 Comments

“P-values overstate the evidence against the null”: legit or fallacious? (revised)

0. July 20, 2014: Some of the comments to this post reveal that using the word “fallacy” in my original title might have encouraged running together the current issue with the fallacy of transposing the conditional. Please see a newly added Section 7.

 

2. J. Berger and Sellke and Casella and R. Berger

Of course it is well-known that for a fixed P-value, with a sufficiently large n, even a statistically significant result can correspond to large posteriors in H0 (Jeffreys-Good-Lindley paradox).  I.J. Good (I don’t know if he was the first) recommended decreasing the required P-value as n increases, and had a formula for it. A more satisfactory route is to ensure the interpretation takes account of the (obvious) fact that with a fixed P-value and increasing n, the test is more and more sensitive to discrepancies–much as is done with lower/upper bounds of confidence intervals. For some rules of thumb see Section 5.

The JGL result is generalized in J. Berger and Sellke (1987). They make out the conflict between P-values and Bayesian posteriors by considering the two sided test of the Normal mean, H0: μ = μ0 versus H1: μ ≠ μ0 .

“If n = 50…, one can classically ‘reject H0 at significance level p = .05,’ although Pr (H0|x) = .52 (which would actually indicate that the evidence favors H0).” (Berger and Sellke, 1987, p. 113).

If n = 1000, a result statistically significant at the .05 level leads to a posterior to the null going from .5 to .82!

While from their Bayesian perspective, this appears to supply grounds for denying P-values are adequate for assessing evidence, significance testers rightly balk at the fact that using the recommended priors allows highly significant results to be interpreted as no evidence against the null–or even evidence for it!

From J. Berger and T. Selke (1987) “Testing a Point Null Hypothesis,” JASA 82(397) : 113.

Many think this shows that the P-value ‘overstates evidence against a null’ because it claims to use an ‘impartial’ Bayesian prior probability assignment of .5 to H0, the remaining .5 spread out over the alternative parameter space. (But see the justification Berger and Sellke give in Section 3. A Dialogue.) Casella and R. Berger (1987) charge that the problem is not P-values but the high prior, and that “concentrating mass on the point null hypothesis is biasing the prior in favor of Has much as possible” (p. 111) whether in 1 or 2-sided tests. Note, too, the conflict with confidence interval reasoning since the null value (here it is 0) lies outside the corresponding confidence interval (Mayo 2005). See Senn’s very interesting points on this same issue in his letter (to Goodman) here.

^^^^^^^^^^^^^^^^^

3. A Dialogue (ending with a little curiosity in J. Berger and Sellke):

So a guy is fishing in Lake Elba, and a representative from the EPA (Elba Protection Association) points to notices that mean toxin levels in fish were found to exceed the permissible mean concentration, set at 0.

EPA Rep: We’ve conducted two studies (each with random sample of 100 fish) showing statistically significant concentrations of toxin, at low P-values, e.g., .02. 

P-Value denier: I deny you’ve shown evidence of high mean toxin levels; P-values exaggerate the evidence against the null.

EPA Rep: Why is that?

P-value denier: If I update the prior of .5 that I give to the null hypothesis (asserting toxin levels are of no concern), my posterior for H0 is still not all that low, not as low as .05 for sure.

EPA Rep: Why do you assign such a high prior probability to H0?

P-value denier: If I gave H0 a value lower than .5, then, if there’s evidence to reject H0 , at most I would be claiming an improbable hypothesis has become more improbable. Who would be convinced by the statement ‘I conducted a Bayesian test of H0, assigning prior probability .1 to H0, and my conclusion is that Hhas posterior probability .05 and should be rejected’?

The last sentence is a direct quote from Berger and Sellke!

There’s something curious in assigning a high prior to the null H0–thereby making it harder to reject (or find evidence against) H0–and then justifying the assignment by saying it ensures that, if you do reject H0, there will be a meaningful drop in the probability of H0. What do you think of this?

^^^^^^^^^^^^^^^^^^^^

4. The real puzzle.

I agree with J. Berger and Sellke that we should not “force agreement”. What’s puzzling to me is why it would be thought that an account that manages to evaluate how well or poorly tested hypotheses are–as significance tests can do–would want to measure up to an account that can only give a comparative assessment (be they likelihoods, odds ratios, or other) [ii]. From the perspective of the significance tester, the disagreements between (audited) P-values and posterior probabilities are an indictment, not of the P-value, but of the posterior, as well as the Bayes ratio leading to the disagreement (as even one or two Bayesians appear to be coming around to realize, e.g., Bernardo 2011, 58-9). Casella and R. Berger show that for sensible priors with one-sided tests, the P-value can be “reconciled” with the posterior, thereby giving an excellent retort to J. Berger and Sellke. Personally, I don’t see why an error statistician would wish to construe the P-value as how “believe worthy” or “bet worthy” statistical hypotheses are. Changing the interpretation may satisfy J. Berger’s call for “an agreement on numbers” (and never mind philosophies), but doing so precludes the proper functioning of P-values, confidence levels, and other error probabilities. And “what is the intended interpretation of the prior, again?” you might ask. Aside from the subjective construals (of betting and belief, or the like), the main one on offer (from the conventionalist Bayesians) is that the prior is undefined and is simply a way to compute a posterior. Never mind that they don’t agree on which to use. Your question should be: “Please tell me: how does a posterior, based on an undefined prior used solely to compute a posterior, become “the” measure of evidence that we should aim to match?” 

^^^^^^^^^^^^^^^^

5. (Crude) Benchmarks for taking into account sample size:

Throwing out a few numbers may give sufficient warning to those inclined to misinterpret statistically significant differences at a given level but with varying sample sizes (please also search this blog [iii]). Using the familiar example of Normal testing with T+ :

H0: μ ≤ 0 vs. H1: μ > 0.  

Let σ = 1, n = 25, so σx= (σ/√n).

For this exercise, fix the sample mean M to be just significant at the .025 level for a 1-sided test, and vary the sample size n. In one case, n = 100, in a second, n = 1600. So, for simplicity, using the 2-standard deviation cut-off:

m0 = 0 + 2(σ/√n).

With stat sig results from test T+, we worry about unwarranted inferences of form:  μ > 0 + γ.

Some benchmarks:

 * The lower bound of a 50% confidence interval is 2(σ/√n). So there’s quite lousy evidence that μ > 2(σ/√n) (the associated severity is .5).

 *The lower bound of the 93% confidence interval is .5(σ/√n). So there’s decent evidence that μ > .5(σ/√n) (The associated severity is .93).

 *For n = 100, σ/√n = .1 (σ= 1); for n = 1600, σ/√n = .025

 *Therefore, a .025 stat sig result is fairly good evidence that μ > .05, when n = 100; whereas, a .025 stat sig result is quite lousy evidence that μ > .05, when n = 1600.

You’re picking up smaller and smaller discrepancies as n increases, when P is kept fixed. Taking the indicated discrepancy into account avoids erroneous construals and scotches any “paradox”.

^^^^^^^^^^

6. “The Jeffreys-Lindley Paradox and Discovery Criteria in High Energy Physics” (Cousins, 2014)

Robert Cousins, a HEP physicist willing to talk to philosophers and from whom I am learning about statistics in the Higgs discovery, illuminates the key issues, models and problems in his paper with that title. (The reference to Bernardo 2011 that I had in mind in Section 4 is cited on p. 26 of Cousins 2014).

^^^^^^^^^^^^^^^^^^^^^^^^^^

7. July 20, 2014: There is a distinct issue here….That “P-values overstate the evidence against the null” is often stated as an uncontroversial “given”. In calling it a “fallacy”, I was being provocative. However, in dubbing it a fallacy, some people assumed I was referring to one or another well-known fallacies, leading them to guess I was referring to the fallacy of confusing P(E|H) with P(H|E)—what some call the “prosecutor’s fallacy”. I wasn’t. Nor are Berger and Sellke committing a simple blunder of transposing conditionals. If they were, Casella and Berger would scarcely have needed to write their reply to point this out. So how shall we state the basis for the familiar criticism that P-values overstate evidence against (a null)?  I take it that the criticism goes something like this:

The problem with using a P-value to assess evidence against a given null hypothesis H0 is that it tends to be smaller, even much smaller, than an apparently plausible posterior assessment of H0, given data x (especially as n increases).  The mismatch is avoided with a suitably tiny P-value, and that’s why many recommend this tactic. [iv] Yet I say the correct answer to the question in my (new) title is: “fallacious”. It’s one of those criticisms that have not been thought through carefully, but rather repeated based on some well-known articles.

[i] We assume the P-values are “audited”, that they are not merely “nominal”, but are “actual” P-values. Selection effects, cherry-picking and other biases would alter the error probing capacity of the tests, and thus the purported P-value would fail the audit.

[ii] Note too that the comparative assessment will vary depending on the “catchall”.

[iii] See for example:

Section 6.1 “fallacies of rejection“.
Slide #8 of Spanos lecture in our seminar Phil 6334.

 [iv] So we can also put aside for the moment the issue of P-values not being conditional probabilities to begin with. We can also (I hope) distinguish another related issue, which requires a distinct post: using ratios of frequentist error probabilities, e.g., type 1 errors and power, to form a kind of “likelihood ratio” in a screening computation.

 

References (minimalist)

Berger, J. O. and Sellke, T.  (1987). “Testing a point null hypothesis: The irreconcilability of p values and evidence,” (with discussion). J. Amer. Statist. Assoc. 82: 112–139.

Cassella G. and Berger, R..  (1987). “Reconciling Bayesian and Frequentist Evidence in the One-sided Testing Problem,” (with discussion). J. Amer. Statist. Assoc. 82 106–111, 123–139.

Blog posts:

Comedy Hour at the Bayesian Retreat: P-values versus Posteriors.
Highly probable vs highly probed: Bayesian/ error statistical differences.

 

 

Categories: Bayesian/frequentist, CIs and tests, fallacy of rejection, highly probable vs highly probed, P-values, Statistics | 71 Comments

Higgs discovery two years on (2: Higgs analysis and statistical flukes)

Higgs_cake-sI’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.  Continue reading

Categories: Higgs, highly probable vs highly probed, P-values, Severity, Statistics | 13 Comments

Higgs Discovery two years on (1: “Is particle physics bad science?”)

Higgs_cake-s

July 4, 2014 was the two year anniversary of the Higgs boson discovery. As the world was celebrating the “5 sigma!” announcement, and we were reading about the statistical aspects of this major accomplishment, I was aghast to be emailed a letter, purportedly instigated by Bayesian Dennis Lindley, through Tony O’Hagan (to the ISBA). Lindley, according to this letter, wanted to know:

“Are the particle physics community completely wedded to frequentist analysis?  If so, has anyone tried to explain what bad science that is?”

Fairly sure it was a joke, I posted it on my “Rejected Posts” blog for a bit until it checked out [1]. (See O’Hagan’s “Digest and Discussion”) Continue reading

Categories: Bayesian/frequentist, fallacy of non-significance, Higgs, Lindley, Statistics | Tags: , , , , , | 4 Comments

Winner of June Palindrome Contest: Lori Wike

photo

.

Winner of June 2014 Palindrome Contest: First Second* Time Winner! Lori Wike

*Her April win is here

Palindrome:

Parsec? I overfit omen as Elba sung “I err on! Oh, honor reign!” Usable, sane motif revoices rap.

The requirement: A palindrome with Elba plus overfit. (The optional second word: “average” was not needed to win.)

Bio:

Lori Wike is principal bassoonist of the Utah Symphony and is on the faculty of the University of Utah and Westminster College. She holds a Bachelor of Music degree from the Eastman School of Music and a Master of Arts degree in Comparative Literature from UC-Irvine.

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Categories: Announcement, Palindrome | Leave a comment

Some ironies in the ‘replication crisis’ in social psychology (4th and final installment)

freud mirror espThere are some ironic twists in the way social psychology is dealing with its “replication crisis”, and they may well threaten even the most sincere efforts to put the field on firmer scientific footing–precisely in those areas that evoked the call for a “daisy chain” of replications. Two articles, one from the Guardian (June 14), and a second from The Chronicle of Higher Education (June 23) lay out the sources of what some are calling “Repligate”. The Guardian article is “Physics Envy: Do ‘hard’ sciences hold the solution to the replication crisis in psychology?”

The article in the Chronicle of Higher Education also gets credit for its title: “Replication Crisis in Psychology Research Turns Ugly and Odd”. I’ll likely write this in installments…(2nd, 3rd , 4th)

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The Guardian article answers yes to the question “Do ‘hard’ sciences hold the solution“:

Psychology is evolving faster than ever. For decades now, many areas in psychology have relied on what academics call “questionable research practices” – a comfortable euphemism for types of malpractice that distort science but which fall short of the blackest of frauds, fabricating data.
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Categories: junk science, science communication, Statistical fraudbusting, Statistics | 53 Comments

Sir David Hendry Gets Lifetime Achievement Award

images-17Sir David Hendry, Professor of Economics at the University of Oxford [1], was given the Celebrating Impact Lifetime Achievement Award on June 8, 2014. Professor Hendry presented his automatic model selection program (Autometrics) at our conference, Statistical Science and Philosophy of Science (June, 2010) (Site is here.) I’m posting an interesting video and related links. I invite comments on the paper Hendry published, “Empirical Economic Model Discovery and Theory Evaluation,” in our special volume of Rationality, Markets, and Morals (abstract below). [2]

One of the world’s leading economists, INET Oxford’s Prof. Sir David Hendry received a unique award from the Economic and Social Research Council (ESRC)…
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Categories: David Hendry, StatSci meets PhilSci | Tags: | Leave a comment

Blog Contents: May 2014

metablog old fashion typewriter

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May 2014

(5/1) Putting the brakes on the breakthrough: An informal look at the argument for the Likelihood Principle

(5/3) You can only become coherent by ‘converting’ non-Bayesianly

(5/6) Winner of April Palindrome contest: Lori Wike

(5/7) A. Spanos: Talking back to the critics using error statistics (Phil6334)

(5/10) Who ya gonna call for statistical Fraudbusting? R.A. Fisher, P-values, and error statistics (again)

(5/15) Scientism and Statisticism: a conference* (i) Continue reading

Categories: blog contents, Metablog, Statistics | Leave a comment

Big Bayes Stories? (draft ii)

images-15“Wonderful examples, but let’s not close our eyes,”  is David J. Hand’s apt title for his discussion of the recent special issue (Feb 2014) of Statistical Science called Big Bayes Stories” (edited by Sharon McGrayne, Kerrie Mengersen and Christian Robert.) For your Saturday night/ weekend reading, here are excerpts from Hand, another discussant (Welsh), scattered remarks of mine, along with links to papers and background. I begin with David Hand:

 [The papers in this collection] give examples of problems which are well-suited to being tackled using such methods, but one must not lose sight of the merits of having multiple different strategies and tools in one’s inferential armory.(Hand [1])_

…. But I have to ask, is the emphasis on ‘Bayesian’ necessary? That is, do we need further demonstrations aimed at promoting the merits of Bayesian methods? … The examples in this special issue were selected, firstly by the authors, who decided what to write about, and then, secondly, by the editors, in deciding the extent to which the articles conformed to their desiderata of being Bayesian success stories: that they ‘present actual data processing stories where a non-Bayesian solution would have failed or produced sub-optimal results.’ In a way I think this is unfortunate. I am certainly convinced of the power of Bayesian inference for tackling many problems, but the generality and power of the method is not really demonstrated by a collection specifically selected on the grounds that this approach works and others fail. To take just one example, choosing problems which would be difficult to attack using the Neyman-Pearson hypothesis testing strategy would not be a convincing demonstration of a weakness of that approach if those problems lay outside the class that that approach was designed to attack.

Hand goes on to make a philosophical assumption that might well be questioned by Bayesians: Continue reading

Categories: Bayesian/frequentist, Honorary Mention, Statistics | 62 Comments

“Statistical Science and Philosophy of Science: where should they meet?”

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Four score years ago (!) we held the conference “Statistical Science and Philosophy of Science: Where Do (Should) They meet?” at the London School of Economics, Center for the Philosophy of Natural and Social Science, CPNSS, where I’m visiting professor [1] Many of the discussions on this blog grew out of contributions from the conference, and conversations initiated soon after. The conference site is here; my paper on the general question is here.[2]

My main contribution was “Statistical Science Meets Philosophy of Science Part 2: Shallow versus Deep Explorations” SS & POS 2. It begins like this: 

1. Comedy Hour at the Bayesian Retreat[3]

 Overheard at the comedy hour at the Bayesian retreat: Did you hear the one about the frequentist… Continue reading

Categories: Error Statistics, Philosophy of Statistics, Severity, Statistics, StatSci meets PhilSci | 23 Comments

A. Spanos: “Recurring controversies about P values and confidence intervals revisited”

A SPANOS

Aris Spanos
Wilson E. Schmidt Professor of Economics
Department of Economics, Virginia Tech

Recurring controversies about P values and confidence intervals revisited*
Ecological Society of America (ESA) ECOLOGY
Forum—P Values and Model Selection (pp. 609-654)
Volume 95, Issue 3 (March 2014): pp. 645-651

INTRODUCTION

The use, abuse, interpretations and reinterpretations of the notion of a P value has been a hot topic of controversy since the 1950s in statistics and several applied fields, including psychology, sociology, ecology, medicine, and economics.

The initial controversy between Fisher’s significance testing and the Neyman and Pearson (N-P; 1933) hypothesis testing concerned the extent to which the pre-data Type  I  error  probability  α can  address the arbitrariness and potential abuse of Fisher’s post-data  threshold for the value. Continue reading

Categories: CIs and tests, Error Statistics, Fisher, P-values, power, Statistics | 32 Comments

“The medical press must become irrelevant to publication of clinical trials.”

pmed0020138g001“The medical press must become irrelevant to publication of clinical trials.” So said Stephen Senn at a recent meeting of the Medical Journalists’ Association with the title: “Is the current system of publishing clinical trials fit for purpose?” Senn has thrown a few stones in the direction of medical journals in guest posts on this blog, and in this paper, but it’s the first I heard him go this far. He wasn’t the only one answering the conference question “No!” much to the surprise of medical journalist Jane Feinmann, whose article I am excerpting:

 So what happened? Medical journals, the main vehicles for publishing clinical trials today, are after all the ‘gatekeepers of medical evidence’—as they are described in Bad Pharma, Ben Goldacre’s 2012 bestseller. …

… The Alltrials campaign, launched two years ago on the back of Goldacre’s book, has attracted an extraordinary level of support. … Continue reading

Categories: PhilPharma, science communication, Statistics | 5 Comments

Stephen Senn: Blood Simple? The complicated and controversial world of bioequivalence (guest post)

Stephen SennBlood Simple?
The complicated and controversial world of bioequivalence

by Stephen Senn*

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Those not familiar with drug development might suppose that showing that a new pharmaceutical formulation (say a generic drug) is equivalent to a formulation that has a licence (say a brand name drug) ought to be simple. However, it can often turn out to be bafflingly difficult[1]. Continue reading

Categories: bioequivalence, confidence intervals and tests, PhilPharma, Statistics, Stephen Senn | 22 Comments

What have we learned from the Anil Potti training and test data fireworks ? Part 1 (draft 2)

toilet-fireworks-by-stephenthruvegas-on-flickr

Over 100 patients signed up for the chance to participate in the clinical trials at Duke (2007-10) that promised a custom-tailored cancer treatment spewed out by a cutting-edge prediction model developed by Anil Potti, Joseph Nevins and their team at Duke. Their model purported to predict your probable response to one or another chemotherapy based on microarray analyses of various tumors. While they are now described as “false pioneers” of personalized cancer treatments, it’s not clear what has been learned from the fireworks surrounding the Potti episode overall. Most of the popular focus has been on glaring typographical and data processing errors—at least that’s what I mainly heard about until recently. Although they were quite crucial to the science in this case,(surely more so than Potti’s CV padding) what interests me now are the general methodological and logical concerns that rarely make it into the popular press. Continue reading

Categories: science communication, selection effects, Statistical fraudbusting | 33 Comments

Allan Birnbaum, Philosophical Error Statistician: 27 May 1923 – 1 July 1976

27 May 1923-   1 July 1976

Today is Allan Birnbaum’s Birthday. Birnbaum’s (1962) classic “On the Foundations of Statistical Inference” is in Breakthroughs in Statistics (volume I 1993).  I’ve a hunch that Birnbaum would have liked my rejoinder to discussants of my forthcoming paper (Statistical Science): Bjornstad, Dawid, Evans, Fraser, Hannig, and Martin and Liu. I hadn’t realized until recently that all of this is up under “future papers” here [1]. You can find the rejoinder: STS1404-004RA0-2. That takes away some of the surprise of having it all come out at once (and in final form). For those unfamiliar with the argument, at the end of this entry are slides from a recent, entirely informal, talk that I never posted, as well as some links from this blog. Happy Birthday Birnbaum! Continue reading

Categories: Birnbaum, Birnbaum Brakes, Likelihood Principle, Statistics | Leave a comment

Blog Table of Contents: March and April 2014

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BLOG Contents: March and April 2014
Compiled by Jean Miller and Nicole Jinn

March 2014

(3/1) Cosma Shalizi gets tenure (at last!) (metastat announcement)

(3/2) Significance tests and frequentist principles of evidence: Phil6334 Day #6

(3/3) Capitalizing on Chance (ii)

(3/4) Power, power everywhere–(it) may not be what you think! [illustration]

(3/8) Msc kvetch: You are fully dressed (even under you clothes)? Continue reading

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The Science Wars & the Statistics Wars: More from the Scientism workshop

images-11-1Here are the slides from my presentation (May 17) at the Scientism workshop in NYC. (They’re sketchy since we were trying for 25-30 minutes.) Below them are some mini notes on some of the talks.

Now for my informal notes. Here’s a link to the Speaker abstracts;the presentations may now be found at the conference site here. Comments, questions, and corrections are welcome. Continue reading

Categories: evidence-based policy, frequentist/Bayesian, Higgs, P-values, scientism, Statistics, StatSci meets PhilSci | 11 Comments

Deconstructing Andrew Gelman: “A Bayesian wants everybody else to be a non-Bayesian.”

At the start of our seminar, I said that “on weekends this spring (in connection with Phil 6334, but not limited to seminar participants) I will post some of my ‘deconstructions of articles”. I began with Andrew Gelman‘s note  “Ethics and the statistical use of prior information”[i], but never posted my deconstruction of it. So since it’s Saturday night, and the seminar is just ending, here it is, along with related links to Stat and ESP research (including me, Jack Good, Persi Diaconis and Pat Suppes). Please share comments especially in relation to current day ESP research. Continue reading

Categories: Background knowledge, Gelman, Phil6334, Statistics | 35 Comments

Scientism and Statisticism: a conference* (i)

images-11A lot of philosophers and scientists seem to be talking about scientism these days–either championing it or worrying about it. What is it? It’s usually a pejorative term describing an unwarranted deference to the so-called scientific method over and above other methods of inquiry. Some push it as a way to combat postmodernism (is that even still around?) Stephen Pinker gives scientism a positive spin (and even offers it as a cure for the malaise of the humanities!)[1]. Anyway, I’m to talk at a conference on Scientism (*not statisticism, that’s my word) taking place in NYC May 16-17. It is organized by Massimo Pigliucci (chair of philosophy at CUNY-Lehman), who has written quite a lot on the topic in the past few years. Information can be found here. In thinking about scientism for this conference, however, I was immediately struck by this puzzle: Continue reading

Categories: Announcement, PhilStatLaw, science communication, Statistical fraudbusting, StatSci meets PhilSci | Tags: | 15 Comments

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