# Between the Devil and the Deep Blue Sea: Tensions Between Scientific Judgement and Statistical Model Selection

## Abstract

Discussions of model selection in the psychological literature typically frame the issues as a question of statistical inference, with the goal being to determine which model makes the best predictions about data. Within this setting, advocates of leave-one-out cross-validation and Bayes factors disagree on precisely which prediction problem model selection questions should aim to answer. In this comment, I discuss some of these issues from a scientific perspective. What goal does model selection serve when all models are known to be systematically wrong? How might “toy problems” tell a misleading story? How does the scientific goal of explanation align with (or differ from) traditional statistical concerns? I do not offer answers to these questions, but hope to highlight the reasons why psychological researchers cannot avoid asking them.

## Keywords

Model selection Science StatisticsModel selection seems to be an evergreen topic in mathematical psychology. Given two or more competing theories about the world, each instantiated as parameterised computational models that provide different accounts of a data set, how should we decide which model is better supported by the data? Typically we formulate this as a statistical inference problem, with various authors arguing for Bayes factors (e.g. Wagenmakers 2007), minimum description length (e.g. Grünwald 2007), cross-validation (e.g. Browne 2000) and a variety of other possibilities besides. To highlight the behaviour of different model selection methods, we often consider “toy problems”, simplified versions of serious inferential scenarios designed to elicit different intuitions about whether the model selection procedure behaves sensibly. The large-sample results presented by Gronau and Wagenmakers (2018) fall within this tradition, highlighted by the Dennis Lindley quote that motivates the work. The results are perhaps unsurprising given the known inconsistency of orthodox cross-validation estimators (Shao 1993), but there is value in highlighting the issue to a broader audience and noting that a Bayesian formulation does not remove this limitation. To the extent that some psychologists are unaware of the need for care when using cross-validation methods—as indeed they may be unaware of a need for caution with respect to Bayes factors or any other model selection procedure—the paper strikes me as helpful and timely.

As much as I enjoyed the paper, I wonder whether the simplicity of exposition comes at a cost. As Vehtari et al. (2018) note in their commentary, Gronau and Wagenmakers’ examples apply leave-one-out cross-validation in a fashion that is rather at odds with how its advocates recommend that it be used. The original paper constitutes a strong argument against naive or accidental misuse of some cross-validation procedures, but the implications for best practice seem much less obvious. Noting that other commenters have discussed technical issues in detail, my goal in this paper is to take a slightly broader view on the tensions between scientific judgement and statistical model selection.

## Mistaking the Map for the Territory

*only*solve simple problems, we may never learn how to think about the complex ones. As someone who has tried to use many different model selection tools over the years, I am of the view that the behaviour of a selection procedure applied to toy problems is a poor proxy for the inferential problems facing scientists. As such, if we are to motivate our approach to model selection by quoting famous statisticians, my preference would be to start with George Box’s (1976, p. 792) comment on the dangers of selective worrying:

Since all models are wrong the scientist must be alert to what is importantly wrong. It is inappropriate to be concerned about mice when there are tigers abroad.

Everyone who develops model selection tools is of course aware that all models are wrong. Scientists do not fully understand the phenomena we are studying (else why study them?) and every formal model-based description of the phenomenon is wrong in an unknown, systematic fashion. One consequence of this, I think, is that while it is usually easy to construct artificial scenarios in which any given procedure misbehaves, it is often difficult to know what implications they might have for the real world scientific problems they approximate.

To illustrate how easy it is to tell a misleading story, consider the behaviour of the Bayes factor—a procedure I presume Gronau and Wagenmakers would endorse as sensible—when presented with a minor variation of their Example 1. In this scenario, there are two models, a “general law” \(\mathcal {M}_{1}\) which asserts that a Bernouilli probability *𝜃* equals 1 and an “unknown quantity” model \(\mathcal {M}_{2}\) that expresses uncertainty by placing a uniform Beta(1,1) prior over *𝜃*. Given a sample *n* successes (i.e. all observations are 1) the Bayes factor will select \(\mathcal {M}_{1}\) with certainty as *n* →*∞*, and the variant of leave-one-out cross-validation they discuss does not. The behaviour of the Bayes factor seems desirable insofar as \(\mathcal {M}_{1}\) is the true model in this scenario. However, it is not difficult to reverse this intuition and construct an example where this same certainty seems *un* desirable.

*almost*correct: the general law holds, apart from a single failure. The probability of success is 1, in the sense that one failure (or indeed any finite number of failures) in an infinite sequence of successes forms a set of measure zero. The true probability of success in a frequentist sense is lim

*n*→

*∞*(

*n*− 1)/

*n*= 1, and similarly, the posterior expected value of

*𝜃*for the unknown quantity model \(\mathcal {M}_{2}\) converges on

*𝜃*= 1 in the large-sample limit. In any sense that a pragmatic scientist would care about, the general law would count as the “correct” account for the phenomenon.

^{1}Nevertheless, the general law model \(\mathcal {M}_{1}\) does not have support at the data

*. So while*

**x***P*(

*|*

**x**_{1}) = 0 for all

*n*after the single failure has occurred, \(\mathcal {M}_{2}\) assigns positive prior probability to the data

*P*(

*|*

**x**_{1})/

*P*(

*|*

**x**_{2}) is therefore 0, and selects

*against*the general law

_{1}with certainty even though

_{1}makes an “almost exactly true” prior prediction, whereas

_{2}assigns the same degree of prior belief to the true rule

*𝜃*= 1 as it does to the exact opposite rule,

*𝜃*= 0.

To a statistician, the reason for this misbehaviour is obvious, and rather boring: a general law formulated as a model that does not accommodate measurement error (and therefore lacks support across most of the sample space) will behave poorly in a world such as our own that actually does have such errors. The fact that the Bayes factor produces counterintuitive inferences when asked to choose between extremely bad models is not prima facie evidence that we should discard Bayes factors. Rather, it requires that we recognise that Bayes factors can produce strange answers when none of the models are “true”. In this instance, the problem arises because the large-sample behaviour of the Bayes factor is to select the model whose prior predictive distribution *P*(* x*|) is closest in Kullback-Leibler divergence to the true data generating mechanism,

^{2}and this is often

*not*the criterion that a scientist cares about. In real life none of us would choose

_{2}over

_{1}in this situation, because from our point of view the general law model is actually “closer” to the truth than the uninformed model. Because Kullback-Leibler divergence is sometimes a poor proxy for sensible judgement, the scientist would (quite correctly) disregard the Bayes factor and make the sensible choice. Importantly though, the fact that the Bayes factor does something unhelpful in a contrived example designed to make it misbehave tells us very little—one way or the other—about whether it is useful in real life. The example I chose is silly, and its evidentiary value is minimal.

Viewed more generally, I find it difficult to know how to apply simple examples to real-world problems. There are no shortage of illustrations that particular model selection procedures misbehave when applied to problems they are not built to solve. For instance, in one of my early papers (Navarro 2004), I documented an issue with (a specific version of) the minimum description length criterion developed by Rissanen (1996) and introduced to psychology by Pitt et al. (2002). The particular issue, in which it is possible for a nested model to be judged *more complex* than the encompassing model, arose when trying to solve an actual psychological model selection problem (see Navarro et al. 2004) in which we compared an exponential forgetting function *y* = *a* exp(−*b**t*) to the strength-resistance model *y* = *a* exp(−*b**t*^{w}) proposed by Wickelgren (1972) and several other models besides. Given that the exponential function is a special case of the strength-resistance model, it is logically impossible for it to be more complex, and the behaviour of the minimum description length criterion here is self-evidently absurd. Does that mean that this criterion is “worse” than simpler criteria such as such as AIC (Akaike 1973) and BIC (Schwarz 1978), in which model complexity is assessed simply by counting the number of parameters? To me, this seems the wrong lesson to draw, given that AIC and BIC both have numerous flaws of their own. Fault can be found with *any* formal criterion for statistical inference, as is nicely illustrated by the many documented concerns with *p* values listed in the psychological literature going back at least to Edwards et al. (1963). As any survey of the statistical literature will reveal (e.g. Vehtari and Ojanen 2012), even the basic desiderata for what model selection is supposed to accomplish are not agreed upon. Viewed from this perspective, showing that a particular procedure behaves strangely in an artificial scenario is not without value, but one should be wary of reading too much into such demonstrations.

## Escaping Mice to Be Beset by Tigers

*scientific*model selection questions are addressable with statistical tools. If scientific reasoning necessarily takes place in a world where all our models are systematically wrong in some sense (often referred to as the -open case), what do we hope to achieve by “selecting” a model? To me, it seems that much of this is tied to the question of what we consider the function of a model to be. In considering this question Bernardo and Smith (2000, p. 238) write

Many authors …highlight a distinction between what one might call

scientificandtechnologicalapproaches to models. The essence of the dichotomy is that scientists are assumed to seekexplanatorymodels, which aim at providing insight into and understanding of the “true” mechanisms of the phenomenon under study; whereas technologists are content withempiricalmodels, which are not concerned with the “truth”, but simply providing a reliably basis for practical action in predicting and controlling phenomena of interest.

Under a “technological view”, the primary role of a model is *predictive*, though the prediction problem differs depending on which methods one prefers. For example, under the Bayes factor approach, a model is identified with its prior predictive distribution *P*(* x*|), whereas under a cross-validation approach one is more likely to focus on the posterior predictive distribution

*P*(

**x**^{′}|

*,), where*

**x**

**x**^{′}represents future data drawn from the (unknown) true distribution. Nevertheless, in both cases, the primary role of a model is operationalised in terms of predictions about data. In contrast to the predictive perspective, the “scientific view” as described by Bernardo and Smith (2000) places more emphasis on the interpretability and explanatory value of

*P*(

*|*

**x***𝜃*,). Ultimately, Bernardo and Smith (2000) conclude that the distinction is not especially important: if scientific models are evaluated on their ability to make predictions, then the “scientific view” reduces to the “technological view” for most intents and purposes.

My view is a little different. It strikes me as notable that statistics papers typically define the term “generalisation” in a way that differs markedly from how psychologists define the term when studying human inductive reasoning (e.g. Lake et al. 2015). In the statistical context, predictive generalisation performance is typically assessed with respect to test data sampled from the *same* process as the training data (e.g. Vehtari and Ojanen 2012). In the literature on human reasoning, however, generalisation is typically assessed by examining how people think about test items that are *systematically different* to the data upon which they were trained, and cannot be (easily) described as realisations of the “same” data generating process from which the training data arose. In my opinion at least, scientific model selections problem seem to have more in common with the latter than with the former. To illustrate this, consider the question of why we consider the Rescorla-Wagner model of Pavlovian conditioning (Rescorla and Wagner 1972) to be such an important milestone in the development of theories of learning. While the model did indeed provide a good account of a range of existing conditioning phenomena, such as blocking (Kamin 1969), overshadowing (Pavlov 1927), conditioned inhibition (Rescorla 1969), and contingency effects (Rescorla 1968), the truly impressive contribution was not the ability to predict new data from replications of these experiments but rather to successfully anticipate new phenomena, such as overexpectation (Lattal and Nakajima 1998) and super conditioning (Rescorla 1971). That is, one of the most important functions of a scientific theory is not simply to predict new data from old experiments, but to encourage directed exploration of new territory, as illustrated by the important role the Rescorla-Wagner model has played in assisting neuroscientists to investigate reward prediction error signals (e.g. Schultz et al. 1997). Curiously, it has sometimes been argued (Devezer et al. under review) that the apparent paradox of scientific progress in the absence of replication (Shiffrin et al. 2018) may be tied to exactly this kind of theory-guided scientific exploration.

It is not that statisticians are unaware of these issues, of course. For example, in a thorough survey on the literature on Bayesian prediction methods, Vehtari and Ojanen (2012, pp. 174–177) characterise the issue very cleanly, by noting that if the training data are all conditioned on specific values * v* for auxiliary or explanatory variables but the test data depend on new values

**v**^{′}, then the prediction problem changes considerably. If the values of

**v**^{′}can differ

*systematically*from the known values

*—as might happen if a researcher with different theoretical views designs a different experiment to one’s own, or the task used to isolate a psychological process changes—I am skeptical that any statistical framing of the problem is any more than an “in principle” solution. None of us are in a position to know what future experiments we or others may run, and estimating the future performance of a model with regards to data collected via unknowable experiments is likely impossible. To pretend otherwise strikes me as a form of what Box (1976, pp. 797–798) referred to as*

**v***mathematistry*: using formal tools to define a statistical problem that differs from the scientific one, solving the redefined problem, and declaring the scientific concern addressed.

To illustrate how poorly even the best of statistical procedures can behave when used to automatically quantify the strength of evidence for a model, I offer the following example. As part of an exercise evaluating category learning models, Lee and Navarro (2002) collected similarity ratings for nine items that varied on two ternary-valued features, shape (circle, square or triangle) and colour (red, green or blue). The optimal multidimensional scaling solution for representing these items was estimated by solving a model order selection problem, using the most reasonable statistical criterion we could think of at the time (see Lee 2001a, 2001b). The estimated solution embeds these nine items within a four-dimensional space: two dimensions are used to represent the colours (i.e. red, green and blue form the vertices of a triangle), and two more are used to represent shape. No more than that is *required* to describe the similarity judgements that people made: as a consequence this stimulus representation ends up being the simplest adequate account of the data and is arguably the statistically “correct” representation to estimate from these data.

Nevertheless, when we used this stimulus representation as part of a categorisation task that used those same stimuli—shifting the context from * v* to

**v**^{′}as it was—categorisation models that relied on this representation to define a measure of stimulus similarity behaved very poorly. These failures did not occur due to a statistical failure in our multidimensional scaling procedure; they arose because of a substantive scientific concern that relates to the difference between the two tasks. The four-dimensional embedding space does not allow dimensional attention rules (e.g. Kruschke 1992) to be applied to

*specific*feature values, because the features themselves are not represented explicitly as

*dimensions*. That is, because “circle-versus-not-circle” is not represented as a primitive feature within this four-dimensional multidimensional scaling solution, a categorisation model that relies on this representation cannot use it as the basis for selective attention, even though human participants do precisely this. To generalise sensibly from the similarity judgement task to the categorisation task, the required representation involved placing the same items on a six-dimensional hypercube

^{3}(i.e. employing six binary-valued features: circle vs not-circle, square vs not-square, etc).

Critically, the reason this seems to happen is that there are factors **v**^{′} that influence the notion of “stimulus similarity” (e.g. learned dimensional attention based on feedback, emphasis on differences between items) that applies in the categorisation task, and these are subtly different to the corresponding factors * v* (e.g. no feedback, emphasis on commonalities among items) that apply to “stimulus similarity” in the direct elicitation task. In other words, because these auxiliary factors differ systematically between the two tasks, even this “simple” generalisation turns out to be difficult and—while statistical measures of the adequacy of different similarity models were undoubtedly useful to us—it is unclear to me how we could have solved this model selection problem as a purely statistical exercise.

## Between the Devil and the Deep Blue Sea

Gronau and Wagenmakers (2018) frame the question of model selection as a perilous dilemma in which one is caught between two beasts from classical mythology, the *Scylla* of overfitting and the *Charybdis* of underfitting. I find myself often on the horns of a quite different dilemma, namely the tension between the *devil* of statistical decision making and the *deep blue sea* of addressing scientific questions. If I have any strong opinion at all on this topic, it is that much of the model selection literature places too much emphasis on the statistical issues of model choice and too little on the scientific questions to which they attach.

To again focus on my own papers rather than criticise others, consider the model fits reported by Hayes et al. (under review). In that paper, we were interested in how people’s inductive reasoning from data is shaped by what they know about the process by which the data were selected, referred to as *sensitivity to sampling* in the literature. This is a theme I have explored across multiple papers in the last several years. To model sensitivity to sampling we relied on earlier work by Tenenbaum and Griffiths (2001), as do most papers I have written on this topic (e.g. Navarro et al. 2012; Ransom et al.2016; Voorspoels et al. 2015). However, the task that we used in the Hayes et al. (under review) paper differs from previous ones in many ancillary respects, and these ancillary details need to be formalised in specific model choices. Some such choices (e.g. how smooth is an unknown generalisation function?) can be instantiated as model parameters, but others (e.g. what class of functions is admissable to describe human generalisation?) are not so simple. I think the choices I made are sensible, but reasonable people might disagree.

*𝜃*and producing a measure of predictive performance. Setting aside the computational details of how one does this, the result is likely to lead to a comparison between model predictions and human performance similar to the one shown in Fig. 1. Even without knowing the particular details of the experiments, the scatterplot showing the fitted model values (

*x*-axis) against the average reponse given by human participants (

*y*-axis) across a large number of experimental conditions strongly suggests that the model fits the empirical data well.

*not*to maximise the correlations as shown in Fig. 1, it was to

*make sense*of the observed generalisation curves shown in Fig. 2. The data in Fig. 2 are the same as those plotted in Fig. 1, but drawn in a way that highlights the empirical effects of theoretical interest. In each column there are multiple generalisation curves shown, plotted separately for each experimental condition, with human data at the top and model predictions at the bottom. It is clear from inspection that the data are highly structured, and that there are systematic patterns to how people’s judgements change across conditions. The scientific question of most interest to me is asking what theoretical principles are required to produce these shifts. Providing a good fit to the data seems of secondary importance. From visual inspection, it is clear that the model captures

*most*patterns in the data, but not all. In particular, looking at the systematic model failure in the second column from the right, the same reader might now be inclined to wonder if I have fallen prey to the Charybdis of

*underfitting*. So which of the mythical beasts, Scylla or Charybdis, have I encountered? Would a cross-validation analysis or Bayes factor calculation tell me? It seems unlikely.

To my mind, the bigger concern here is that to focus too heavily on the issue of under/overfitting is to be seduced by the devil of statistical decision making. When we actually analysed the data, the allure of the deep blue sea of science led us to a different perspective. The approach we took was to ignore the quantitative fits almost entirely, and focus on the extent to which the key *qualitative* patterns in the data are an invariant prediction of the model across different choices of the parameter values *𝜃*. Loosely inspired by the “parameter space partitioning” idea introduced by Pitt et al. (2006), we defined a set of ordinal constraints in the data that any theoretical account would need to explain (e.g. increasing the number of observations caused a crossover effect under property sampling, column 4 from the left), and then showed that under most parameter values in the model, the predictions about these ordinal effects did not change. In other words—to recast this in the “scientific versus technological” language used by Bernardo and Smith (2000)—the scientifically important patterns are captured by *P*(* x*|

*𝜃*,) regardless of the specific value of

*𝜃*.

To my way of thinking, understanding how the qualitative patterns in the empirical data emerge naturally from a computational model of a psychological process is often more scientifically useful than presenting a quantified measure of its performance, but it is the latter that we focus on in the “model selection” literature. Given how little psychologists understand about the varied ways in which human cognition works, and given the artificiality of most experimental studies, I often wonder what purpose is served by quantifying a model’s ability to make precise predictions about every detail in the data. Much as the false confidence of the Bayes factor in the “negligible error” scenario I constructed at the beginning is entirely an artifact of its sensitivity to a bad ancillary assumption made by one of the models (that *𝜃* must be exactly 1 for a general law to hold), it seems to me that in real life, many exercises in which model choice relies too heavily on quantitative measures of performance are essentially selecting models based on their ancillary assumptions. It is unclear to me if this solves a scientific problem of interest.

## Footnotes

- 1.
While there are many people who assert that “a single failure is enough to falsify a theory”, I confess I have not yet encountered anyone willing to truly follow this principle in real life.

- 2.
For instance, Gelman et al. (2003, pp. 586–587) present an analogous convergence result for the posterior distribution

*P*(*𝜃*|*x*) within a single model . The result generalises to the Bayes factor by noting that the Bayes factor identifies a model with the prior predictive distribution*P*(*x*|). Substituting*P*(*x*|) for the role of*P*(*x*|*𝜃*) in their derivation produces the necessary result. - 3.
For the purposes of full disclosure, I should note that the precise situation from Lee and Navarro (2002) is quite a bit more complex than this description implies, and there are several details about how we had to adapt a model from one context to be applicable to the other have been omitted.

## Notes

### Acknowledgements

I am grateful to many people for helpful conversations and comments that shaped this paper, most notably Nancy Briggs, Berna Devezer, Chris Donkin, Olivia Guest, Daniel Simpson, Iris van Rooij and Fred Westbrook.

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