AIC MYTHS AND MISUNDERSTANDINGS
Produced and posted by and . This site will be
Copyright By PowCoder代写 加微信 powcoder
updated occasionally. The site is a commentary; we have not spent a great deal of time
and effort to refine the wording or be comprehensive in any respect. It is informal and
we hope people will benefit from our quick thoughts on various matters.
The most recent changes and additions were on April 12, 2006
Some issues gain an acceptance and have a life of their own, being passed from person to
person as fact, when they are actually incorrect. The model selection literature has a
number of such issues – myths and misunderstandings of a sort. In addition, there might
be honest differences of opinion or philosophy. Here we try to note several of these in
reference to our 2002 Springer-Verlag book or concerning K-L based model selection in
general. The issues noted below are in no particular order.
● AIC is only for comparing 2 models (Harrell, F. E. 2001. Regression modeling
strategies. , , NY.). This statement is simply incorrect and
seems to stand-alone, as we have not seen other comments such as this claim.
● Information-theoretic approaches can only be applied when there is one data set.
This incorrect notion comes from Peery et al. (2004. Applying the declining population
paradigm: diagnosing causes of poor reproduction in the marbled murrelet. Conservation
Biology 18:1008-1098); they state, “… in MCH (multiple competing hypotheses)
multiple data sets are evaluated against predictions from multiple limiting factors,
whereas the method of Burnham and Anderson fits multiple models to one data set.”
Two points can be made here.
First, the authors are confused as to what is meant by a “data set” in the statistical
sciences. The literature is full of examples where more “than one data set” is analyzed
using information-theoretic methods: e.g., distance sampling data over multiple years or
multiple areas or capture-recapture data over two genders or 3 age classes. The most
recent analysis of the data on the northern spotted owl [Anthony et al. Wildlife
Monographs No. 163.] where data from 16 large study areas were analyzed using 2 sex
classes and 3-4 age classes. The notion that only “one data set” can be used in the
information-theoretic (or Bayesian approaches) is incorrect. Stephens et al (2005) make
the same mistake when they state that AIC cannot be used for treatment vs. control data
as “the same data must be used.” Clearly, the treatment and control data constitute one
data set (not 2).
Second, the “…method of Burnham and Anderson…” is also not correct phrasing. The
book by Burnham and Anderson is a synthesis of several world-class scientific
achievements (e.g., Kullback and Leibler 1951 and Akaike 1973); our contributions
include only a careful synthesis of the vast literature on the subject of model selection
and inference. We cannot take credit for the methods now available.
● Two individuals have expressed concern over model averaging to estimate
regression coefficients in linear regression (the βs). There does not seem to be
disagreement over model averaging from prediction; the question relates to averaging the
regression coefficients. Both individuals are aware that the estimate of βi depends on
what other variables are in the model (see Burnham and Anderson pages 180-181 for
examples).
Thus, if one has a particular interest in, say, β2 then one might want to use the simple 3-
parameter model with a slope, regression coefficient on X2 and the residual variance. The
inclusion of other predictor variables influences the estimates of β2 unless all the
predictor variables are orthogonal (which almost never happens unless the data are from
an experiment). Then the estimate of β2 is conditional on the other variables in the
model. The alternative approach is to make an “unconditional” estimate of β2. This
involves model averaging; the resulting estimate is still conditional on the model set.
This approach tries to provide a valid estimate of the effect of X2 on the response variable
without making it conditional on other variables in the model. This is often a useful
approach. Of course, the parameter β2 must mean the same thing in every model – the
slope on the predictor variable X2.
Another point on this same issue is that if a person accepts model-averaged prediction
they are implicitly accepting model-averaged structural regression parameters in linear
models. This is because any model-averaged prediction is identical to the prediction from
the single linear model produced by the model-averaged β’s. (see e.g., Burnham and
Anderson 2002, pages 252-253). If model averaged prediction is “good,” then (certainly
in linear models) model-averaged parameters must also be “good.”
● , University of Oxford, takes issue on several accounts via various web
sites. DRA wrote him asking for clarification (December, 2003) but he chose not to
respond. Several of his statements have been picked up and several people have asked us
about these, so we will try to note his position and ours.
1. AIC assumes a true model. This is not correct; see Chapter 7 of Burnham and
Anderson (2000). This error may come from the fact that there are several
derivations from K-L information to AIC. One such derivation notes that the
deviance (the first term in AIC) has a relationship to the chi-squared distribution
(and is therefore the basis for likelihood ratio tests). The chi-squared distribution
of the test statistic comes about only if the models are nested. We are guessing,
but this might be the source of the confusion. Our clear position on this issue is
that nothing need be assumed about a true model when justifying or using AIC (or
AICc or QAICc); see details in Sections 7.2 and 7.2 of our 2002 book.
2. AIC is only for nested models. This is unfounded. AIC as an estimator of
relative, expected Kullback-Leibler information is for both nested and nonnested
models. We have not seen this claim in others sources; it is simply incorrect.
3. The so-called penalty term in AIC (i.e., 2K) is not a bias correction term.
This is incorrect, see Chapter 7 in Burnham and Anderson (2002). There are
certainly dozens of journal papers that clearly show that the maximized log(L) is a
biased estimator of relative, expected K-L information and that to a first order a
defensible asymptotic bias correction term is K, the number of estimable
parameters in the model. So, E(K-L) = log(L) – K. To obtain his AIC, Akaike
multiplied both terms by –2. Thus, AIC was –2log(L) + 2K. Note, the 2 is not
arbitrary; it is the result of multiplying by –2 such that the first term in the AIC is
the (well known) deviance, a measure of lack of fit of the model.
The rigorous derivation of the estimator of expected relative K-L, without
assuming the model is true, leads to a bias correction term that is the trace of the
product of two matrices: tr(J*I-1). If the model, g, in question is the “true” model,
f, then this trace term equals K. If g is a good (in K-L sense) approximation to f
then tr(J*I-1) is not very different from K. Moreover, any estimator of this trace
(hence, TIC model selection) is so variable (i.e., poor) that its better to take this
trace term as K rather than to estimate it.
4. Ripley states, “Burnham and Anderson (2002) is a book I would recommend
people NOT read until they have read the primary literature. I see no
evidence that the authors have actually read Akaike’s papers.” The first
statement is Dr. Ripley’s opinion and he is certainly entitled to it. The second
statement is simply wrong. We have read all of Akaike’s papers in detail and
have corresponded with him. Our book is full of specific references to Akaike’s
papers. It surely must be clear from our 1998 and 2002 books that we read these
● Guthrey et al. (2005. Information theory in wildlife science: critique and viewpoint.
Journal of Wildlife Management 69:457-465) represents a paper in a special class. This
was an invited paper by , then editor of the Journal of Wildlife
Management. No JWM reviewers are listed or mentioned and we assume that Morrison
handled all details with respect to this manuscript. We have written Morrison and asked
for an invitation to respond to various points made by Guthrey et al. Morrison offered
only a Letter to the Editor, which we did not view as appropriate (or fair – to us or the
science community that JWM serves).
The paper represents a near delirious rant and perhaps cannot be taken seriously. People
are certainly free to critique the various information-theoretic approaches; however, we
submit that those offering a critique should have some basic understanding of the
philosophical and mathematical-technical issues before publishing in an open science
forum (as in the Journal of Wildlife Management). As some scientists have read the
paper by Guthrey et al. we will provide the following material for consideration. We
have noted only a few of the worst aspects here; a full explanation of the problems would
require much more time than we have been willing to spend.
1. In our philosophical view data contain information (if collected according to
some fundamental principles; e.g., a well-founded sampling protocol or experimental
design). Here, we use the word information in a technical sense (Boltzman, Shannon,
and Kullback-Leibler information). Extraction of such information from the data can
take a couple of general forms:
· In simple, often 2-3 dimensional problems, one can extract some information in the
data by plotting or computing simple summary statistics.
· In more interesting/difficult situations (e.g., the real world) models are useful in
extracting the information in the data and allowing an understanding of the issues. This
is broadly termed “model based inference” and has been useful in the empirical sciences,
medicine, and engineering over the past several decades if not centuries.
Model based inference is a huge subject and well accepted; it is basically unavoidable
as well as very powerful. Guthrey et al. seem to almost deny the value (actually the
necessity) of quantification in the empirical sciences. Model based inference begs the
question “which model should be used”as it is rarely clear a priori that one model is
somehow known to be “best.” Further thought begs the further questions about the
technical meaning of “best model.”
Many approaches have been put forward over the past 50-80 years to address the
central issues of “model selection.” It is a historical fact that poor model selection tools
happened to be developed first (e.g., stepwise regression, likelihood ratio tests). Such ad
hoc tools have been used extensively because much better tools were late in coming.
Making matters worse is that these more powerful methods have not been widely taught
by statistics departments, at least to non-majors.
By “much better tools” we are referring to various Bayesian approaches that have
become computationally feasible only in the past 15-20 years, information-theoretic
methods that have been introduced over the past 20-30 years, and various computer
intensive approaches (e.g., cross validation, bootstrapping) in the past 20 or so years.
2. Lack of a fundamental understanding of what Guthery et al. call the “algorithm” is
illustrated by the following (page 459),
“… if the global model is presumably valid, why should it be pared? If
a pared model is presumably valid, why would one advance a presumably
invalid global model?”
The central point is that one does not know a priori which of the R models might be
“presumably valid.” How is one supposed to know that a simple linear model with 8
unknown parameters is “valid” while other models might be nonlinear and have, say, 3-
11 or perhaps 30 unknown parameters? Even if one could determine “presumably valid”
would there not be some uncertainty about this matter? What if two co-investigators
disagreed on the “presumably best model”? What if there is disagreement on the
“presumably best model” in a courtroom situation? Futhermore, it is certainly unclear as
to what Guthery et al. might mean by a “valid” model.
How does sample size play into these technical issues? Should a product multinomial
model with 8 survival probabilities, 8 sampling probabilities and no interaction effects
serve for sample sizes ranging from 120 tagged animals to perhaps 54,000 or 388,000
tagged animals? Clearly one cannot often judge that one model out of many is
“presumably valid” nor would we expect others to agree when there is some level of
controversy involved.
A key issue people often fail to properly comprehend is that our context is that of fitting
models to data to learn what the data “have to tell us” via estimated parameters and the
strength of evidence about the different models themselves. The parameters are not a
priori known. The size of model (number of parameters) that can reliably be fit to given
data depends in part on the sample size, and is not a prior known. In this context
“validity” of a model is not a useful concept. What is important is that fitting the models
to the data should lead to useful and reliable knowledge. Fitting too general a model risks
spurious results; fitting too simple a model risks failing to identify interesting real effects.
The “balance” point is not known a prior and depends on sample size.
These errors in both logic and understanding apply to many simple situations. Consider a
simple control vs. treatment experiment (completely randomized design) which results in
two conceptual models – one with a treatment effect and the other without a treatment
effect. How would a person just say one of these models was “presumably valid”? What
would be the scientific basis for saying “the model with no treatment effect is valid” with
no analysis? Is not science supposed to be about objectivity?
3. Several bold statements by Guthery et al. seem to defy any printable response. These
must include:
“The point is that statistical assumptions serve the artificial world of
statistical theory; real world ecological processes operate largely
independently of statistical assumptions and theory.” (Page 460)
“Contrary to popular opinion, the statistical principle of parsimony
borrows no legitimacy from Ockahm’s Razor, …” (Page 460)
4. Guthery et al. remark,
“How should wildlife scientists address this dizzying array of
information criteria and other model selection approaches?”
These authors are just now starting to raise questions that we hit upon in 1989-90 and
other investigators hit upon much earlier. During 1989-90 we were working with Drs.
Jean- and on the open population capture-recapture
models whereby we had practical problems involving easily 10-30 models with the
number of unknown parameters ranging from perhaps 2 to 60. These models were rarely
nested; hence likelihood ratio tests were uninterpretable. Goodness-of-fit tests were of
little help in understanding and were critically dependent on the arbitrary α–level. Some
models had high precision of estimated model parameters while other models made more
realistic assumptions but precision was sacrificed.
This lead us to the extensive literature on model selection theory and methods. Necessity
lead us to Akaike’s information criterion (AIC). We read and tried to understand why
such a simple equation could be so potentially useful. We completed an Ecological
Monograph (Lebreton et al. 1992) using a mix of null hypothesis testing and Akaike’s
information criterion.
Lebreton and Clobert went on with their research on the open models while we decided
to study the model selection issue more thoroughly. We became aware of the multitude
of alternatives available (see Burnham and Anderson 2002:37 for a brief summary) and
the large technical literature (including several books) on model selection. We did not
write the first edition of our book to blindly showcase AIC over other methods. We
began our 7-8 year research by trying to understand the foundation of each of the model
selection approaches. What assumptions were required in the derivation of the various
approaches? Several papers and books helped to isolate a few good methods (e.g., AIC,
BIC, RIC) while indicating that other approaches were almost universally poor (e.g, R2
stepwise hypothesis testing). We began to understand that there were few mathematical
errors in the literature, but deep differences in philosophy. These philosophical
differences lead to differing approaches and it became important to sort these out in our
first edition (Burnham and Anderson 1998).
We believe there are compelling reasons to use AICc and QAICc as effective methods for
general use. For a given situation, a specialized method can potentially be developed
and might be superior to Akaike’s information-theoretic approach – we do not deny this
(however see the 1998 Springer-Verlag book by McQuarrie and Tsai, Regression and
time series model selection). However, there are, to us, extensive reasons to believe that
AICc and QAICc are at the current state of the science for a general approach. The
statement by Guthrey et al. might have been appropriate in 1990, but not today. How
could these authors have read or understand the material in our 2002 book?
5. Guthery et al. (page 462) state,
“…’Akaike best’ models suggest faulty data whenever the ‘best’ model
does not contain the trivially obvious, such as year effects on the annual
survival of an r-selected species.”
This statement seems to be a farrago. Data analysis can show what inferences the data
support, not the exact nature of full reality. Often year-specific parameterizations are
simply not supported by the data available, particularly when sample size is small (see
Section 3.5 of our book for an example using sage grouse). The 3 best models for the
sage grouse data lacked a year-specific parameterization; but it is incorrect to claim,
therefore, that these data were “faulty.” The use of likelihood ratio tests selected a model
for these sage grouse data with 58 parameters (∆ = 36.3), while AICc selected a
parsimonious model with only 4 parameters. The evidence ratio (K = 4 vs. 58
parameters) was 76 million. Clearly, too much uncertainty (high variances) exists when
trying to estimate 58 unknown year-specific parameters when the data set is fairly sparse.
Still, just because the best model does not contain year-specific parameters is not a
logical basis for claiming that the data are “faulty.” There is an analogy with null
hypthesis testing: failure to reject Ho does not mean the data are faulty nor that the null
hypothesis is true.
6. Kadane and Lazar (2004, JASA, 279-290 – in Guthery’s tirade) state that the
frequentist criteria are ad hoc, having “no guiding principle.” Our strong belief is that
the deep guiding principle is Kullback-Leibler information loss and that methods
stemming from this foundation allow a rigorous theory for model selection as an
approximation to full reality. The Bayesian literature (including BIC) so often assumes
that (1) a true model exists and (2) that it is in the set! This (true model) approach is not
mathematically wrong; but it is philosophically absurd (e.g., once one has found this best
model, are they to think that it represents full reality in all respects
程序代写 CS代考 加微信: powcoder QQ: 1823890830 Email: powcoder@163.com