Astrophysicist Andrew Jaffe pointed me to this and discussion of my philosophy of statistics (which is, in turn, my rational reconstruction of the statistical practice of Bayesians such as Rubin and Jaynes). Jaffe’s summary is fair enough and I only disagree in a few points:

1. Jaffe writes:

Subjective probability, at least the way it is actually used by practicing scientists, is a sort of “as-if” subjectivity — how would an agent reason if her beliefs were reflected in a certain set of probability distributions? This is why when I discuss probability I try to make the pedantic point that all probabilities are conditional, at least on some background prior information or context.

I agree, and my problem with the usual procedures used for Bayesian model comparison and Bayesian model averaging is not that these approaches are subjective but that the particular models being considered don’t make sense. I’m thinking of the sorts of models that say the truth is either A or B or C. As discussed in chapter 6 of BDA, I prefer continuous model expansion to discrete model averaging.

Either way, we’re doing Bayesian inference conditional on a model; I’d just rather do it on a model that I like. There is some relevant statistical analysis here, I think, about how these different sorts of models perform under different real-world situations.

2. Jaffe writes that I view my philosophy as “Popperian rather than Kuhnian.” That’s not quite right. In my paper with Shalizi, we speak of our philosophy as containing elements of Popper, Kuhn, and Lakatos. In particular, we can make a Kuhnian identification of Bayesian inference within a model as “normal science” and model checking and replacement as “scientific revolution.” (From a Lakatosian perspective, I identify various responses to model checks as different forms of operations in a scientific research programme, ranging from exception-handling through modification of the protective belt of auxiliary hypothesis through full replacement of a model.)

3. Jaffe writes that I “make a rather strange leap: deciding amongst any discrete set of parameters falls into the category of model comparison.” This reveals that I wasn’t so clear in stating my position. I’m not saying that a Bayesian such as myself shouldn’t or wouldn’t apply Bayesian inference to a discrete-parameter model. What I was saying is that my philosophy isn’t complete. Direct Bayesian inference is fine with some discrete-parameter models (for example, a dense discrete grid approximating a normal prior distribution) but not for others (for example, discrete models for variable selection, where any given coefficient is either “in” (that is, estimated by least squares with a flat prior) or “out” (set to be exactly zero)). My incoherence is that I don’t really have a clear rule of when it’s OK to do Bayesian model averaging and when it’s not.

As noted in my recent article, I don’t think this incoherence is fatal–all other statistical frameworks I know of have incoherence issues–but it’s interesting.

off-topic

Have you seen this? http://www.nber.org/papers/w16788.pdf

Here the abstract:

A rise in the sex ratio (increasing relative surplus of men in the marriage market) in China and several

other economies, in theory, can simultaneously generate a decline in the real exchange rate (RER)

and a rise in the current account surplus. We demonstrate this logic through both a savings channel

and an effective labor supply channel. In this model, a low RER is not a cause of the current account

surplus, nor is it a consequence of currency manipulations. Empirically, those economies with a high

sex ratio tend to have a low real exchange rate, beyond what can be explained by the Balassa-Samuelson

effect, financial underdevelopment, dependence ratio, and exchange rate regime classifications. Once

these factors are accounted for, the Chinese real exchange rate is estimated to be undervalued by only

a relatively trivial amount.

Since you have made research about sex ratio, I was wondering if you have anything to add, even though as you always say, you studied macroeconomics at 11th grade….

Manoel:

I know too little of macroeconomics to evaluate this paper. And I certainly can't evaluate it statistically: they don't have any scatterplots! A scatterplot would seem essential to me in trying to understand that last sentence in their abstract.

The Kuhnians believe that science jumps irrationally from one fad to another. If someone said that you were not Kuhnian, then that was a complement.

I think the only sense Gelman intends in calling Bayesian

inference "Kuhnian" is the shared assumption that all the members of

the "paradigm" are laid out at the start, and normal science is just

tinkering and puzzle solving within that paradigm. To the extent that introducing a brand new theory requires

recalculating all the priors, "revolutionary science" is non-Kuhnian. Anyone who reads Kuhn carefully will

see he rejects, explicitly, Bayesianism.

But, Gelman should NOT wish to see himself as a Lakatosian, whom

Feyerabend correctly described as a "fellow anarchist". Any research programme, according to

Lakatos, can be defended "progressively" no matter how many anomalies

force adjustments and "worm eaten stays". In short, Lakatos reduces to the worst of Kuhn, which is why

Popper denounced him! Of course

this is not surprising since Lakatos was precisely trying to accommodate Kuhn,

hoping to save something of Popper (e.g., revolutions can occur when the group

in power finally decides to start over with a brand new programme—but it is

NOT the data or evidence that forces this, for Lakatos). Saving a programme progressively is

analogous to retaining a paradigm by tinkering around the "protective

belt" while saving the hard core.

Therefore, if Gelman's approach is not Kuhnian, it also cannot be

Lakatosian, in any interesting sense.