Having Views is Overrated

In this post, I am going to advocate for the position that having (first-order) philosophical views is overrated.  I am going to take for granted that philosophical inquiry involves the pursuit of knowledge and understanding.

There is a model of inquiry, which I think I remember being articulated by Robert Stalnaker, where we start with a figurative sack full of all the possibilities there are, and proceed by trying to empty the sack down to the single possibility that is actually the case.  This model is often described in terms of “locating” oneself in the space of possibilities, and progress in inquiry, on this model, is understood in terms of culling one’s options or ruling out possibilities.

Thinking about inquiry this way tends to suggest that our focus should be on the set of currently live options, and our strategy should be to seek out direct reasons to further narrow that set.  If the set includes rival possibilities A through Z, we should seek out a reason to exclude A from the set, or a reason to exclude B from the set, etc. and once we exclude A from the set, we are done with A: our focus will be on possibilities B through Z.  After all, if we were proceeding correctly in our attempts to winnow down possibilities, A is false.  Why waste our time thinking further about it?

I think that everything I am about to say is, strictly speaking, compatible with this model of inquiry itself.  That is, I don’t think that what I say will require us to jettison this model.  But, what I am going to say is not compatible with the “live option” focus that I just outlined as “suggested” by the model.  This is because I think the best chances for solid philosophical progress will involve rigorous focus on possibilities that are outside the live option set, as well as those within it.

One of the nicest side-effects of specializing in historical philosophy is the requirement that one spend a great deal of one’s time seeking out charitable and/or sympathetic readings of views that one would ordinarily be tempted to dismiss out of hand.  For me, this side-effect has so far been manifested most with respect to interpreting David Hume’s account of cognition and John Locke’s philosophy of language.  These are a pair of views that are routinely dismissed in contemporary discussions of those topics.  So, it is natural to ask why this would be a worthwhile endeavor.

Now, I want to be clear: it is definitely not that I harbor the secret hope that, for example, Hume’s theory of mind is actually correct.  This isn’t about thinking we removed possibilities from the sack prematurely.  Rather, it is that, more valuable than simply knowing that an option is to be culled is acquiring an understanding of why it is to be culled.  What is it that we need from a theory of X, that the culled theory can’t give us?  What features of the culled theory are preventing it from meeting that need?  What amendments or revisions to the theory would be sufficient to meet that need?

Now, David Hume’s theory of cognition is notorious for the sparsity of its resources.  The ambitions of Hume’s theory outstrip those resources to such a degree that it is entirely reasonable, prior to detailed investigation, to judge that Hume’s theory will obviously fall far short of its aims.  But, far from being a reason to dismiss Hume’s theory, this mismatch between ambitions and resources is precisely what makes Hume’s theory a promising target for inquiry. Or, at least, that is part of what I am hoping to argue in this post.

One way in which parsimony can be a theoretical virtue is this: simpler systems/theories are easier to investigate.  For example, if one proposes that all the variety of chemical interactions we observe can be explained by appeal to a single feature of the chemicals in question, which can take any of 3 values, it is far easier for us to exhaust the possibilities covered by such a theory than one which invokes 100 features, each of which can take any of 40 values.  Now antecedently, the former of those theories is far less likely to be right, but it is also far easier to learn about.  We will encounter problems with that theory far sooner, and we will be able to design experiments that could show the theory to be wrong more easily.

For example, Hume’s theory (from the Treatise) treats perceptual experience and cognition as being mental occurrences that are fundamentally of the same kind, and differing only with respect to their degree of “force and vivacity”.  This is a serious constraint on how Hume can attempt to account for the differing features of perceptual experience and cognition.  Which means we should be able to identify potential challenges for his view more easily, and find out which aspects of cognition that we’d like to have an account of Hume’s account is unable to satisfy.

Learning which challenges Hume’s account can’t meet will help us identify the minimal set of resources needed to render his account adequate.  Now, I’ve been writing as though the conditions of adequacy are somehow a given, or something we can take as granted.  But the point remains even if we defer settling that question as well.  What we learn is simply conditional:  If a theory of X needs to account for Y, then it needs to have such-and-such resources. Or, put another way: we learn claims about the consistency or inconsistency of different theses, rather than first order claims about topic X.

I think that learning such things can ground our interest in investigating theories, independent of our attitude towards their truth.  Investigation of Hume’s theory is instrumentally valuable for our ultimate goal of determining the correct theory of cognition.  It can teach us about the range of theories of cognition in relation to particular tasks that one might set out for a theory of cognition.

It is, of course, incidental that Hume is a historical figure.  Contemporary theories that one regards likely to be false can play this same role.  I have never found cognitivism about intention to be an appealing view, but it has a very nice relationship between its ambitions (to explain the norms of practical rationality) and it resources (to draw only on the norms of theoretical rationality).  To me, this means that we should expect to learn a great deal from investigating the view, irrespective of our attitude towards its truth.  In fact, the more skeptical one is about the view, the more they should expect investigations of the view to be informative about what work is really being done by the postulation of intention as a distinctively practical attitude.

Perhaps a briefer way to make my point is this:  One need not have first-order views to discover/produce philosophical positions worth investigating. Neither does one need to have first-order views in order to evaluate the success of those philosophical positions relative to specific aims.  For much of what needs to be done in the course of philosophical inquiry, then, one has no need for first-order views.

There is an interesting question about whether we can do as good of a job defending views that we don’t accept, but I will leave that for another post (to lay my cards on the table, though, I actually suspect that having first order views is, if anything, a hindrance to our capacity for sympathetic interpretation of the alternative positions).

2 Responses to Having Views is Overrated

  1. John says:

    I agree that having first order views is unnecessary. In fact, young philosophers are too often goaded into having them. I blog about related philosophical issues at reasonandmeaning.com

    JGM, PhD

  2. […] I presented my own views on methodology in the Young Philosophers series (available on Youtube), which more or less echo points made in this blog post. […]

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