What follows is an attempt to clarify what I took to be an
obvious point made in a previous post (here).
There is a seriously under appreciated research rule of
thumb (one that I have elevated to Norbert’s first principle): those things not worth doing are not worth
doing well. What makes something worth doing? Well, in syntax (and other
scientific domains as I understand them), what’s worth doing is anything that
will advance understanding. That means
trying to explain why things are the way
they are. Now a way station towards this quest is figuring out how things are, but this is (or in my
view should be) a way station. The big rewards lie with ‘why’ questions. Why are humans such terrific linguistic
machines? Why does syntactic binding require c-command? Why do grammars code
locality conditions? Why does French eschew null subjects but Italian
doesn’t? I take this to be very anodyne. However, it has a pretty big consequence, I
believe. If ‘why’ questions are what
drive inquiry, if they are the cowbell that makes the
tune go, then a very important (supremely important) dimension of research is
the boring/interesting axis. I take this to be obvious, but as the obvious is at
times inaccessible (I always have trouble locating the young woman here?),
let me spell this out a bit more.
‘Why’ questions are interest relative (here). They live in a context
of presuppositions and other interests.
Some ‘why’ questions are BORING and ANNOYING!! If you don’t believe me
find a three year old with whyitis and see how long you last. So, some ‘why’ questions are interesting,
some not. Good research aims to find the first and minimize time spent
(wasted?) on the second.[1] A good rule of thumb is to find an
interesting ‘why’ question and study it. Why? Because the answer that one gets
to an interesting question is quite often interesting. And what makes it
interesting? If true it explains why
what you are asking is the way it is. In
short, the interest of the ‘why’ question carries over to the interest of the
answer. It’s what gives the research cowbell.
If this is correct, then one dimension along which theories
(answers to ‘why’ questions) can be evaluated is wrt their boredom index (BI).
And the rule is: choose topics with low BIs and eschew those with high BIs. Two observations.
First, the BI index of a theory can change over time. As we
explore its properties more fully and understand how it works the explanatory
oomph (this is a technical term EO) goes down.
The more we understand the inner workings of an account the less why-mileage
we get. This follows from the fact that why questions are interest relative and
so are susceptible to change as the knowledge context shifts. What were once
exciting insights based on exciting low BI projects loose EO and recede into
the presupposed background (they become fixed truths!). There is a
thermodynamic rule in fact, BI rises over time, EO dissipates as we make
scientific progress. To keep BI low requires finding hypotheses with high
potential EO and convert these to actual EO. But as we go from potential to
actual EO, BI tends to rise. Of course, really great programs have very high
potential EO and hence very low actual BI and it may take a very long time for
BI to rise to dangerous levels. But, after a while, even the best stories
(indeed those that we take to be obviously true) loose EO and increase BI. Or
to say this pedantically: as the question of interest becomes settled it
becomes less interesting.[2]
Interest relativity is a bitch, aint’ it?
Second, it often takes a lot of time and effort to develop a
story that answers an interesting ‘why’ question. In other words, a central characteristic of
many (most? all?) very low BI questions is that they are hard to come by. However, if they have high EO (there is a
systematic inverse relation between BI and EO, as one goes down the other goes
up, i.e. BI µ
1/EO) then they are very much worth pursuing. However, as high EO low BI
theories are often non-obvious and often appear on surface inspection to be incorrect,
they need a lot of nurturing, e.g. protection from falsificationist sadists.
Third, not all apparent ‘why’ questions are either real
questions or worth pursuing when posed.
As in most things, some why questions that look interesting are pseudo-questions
and even some non pseudo ‘why’ questions are currently unanswerable. In other words, not all frogs are princes and
there is a tide in the affair of ‘why’ questions. Consequently, one thing one
does (or should do) in pursuing a ‘why’ question with high potential EO is see
what it buys you were it true, i.e. look for confirming evidence. As I said (here),
this may involve a falsificationist strategy towards a verificationist
end. Unexpected explanations have high
EO, so it pays to look for them in evaluating a theory’s potential. Similarly, apparent falsification is entirely
expected and is reasonable to ignore.
How long is it reasonable to ignore it? There is, sadly, no, good answer to this. But
we do have cases in which 35-40 years was required to get what we now know to
be the “truth” established (here). This
means that, sadly, judgment is required in deciding what to do. And different
reasonable people (oh yes there are also unreasonable ones, and they should be
ignored. Sadly, they are hard to identify: were that they all looked froggish
when being unreasonable, sigh!) judge differently and pursue different
directions. Often when one hears methodological dicta about falsification etc.
it just signals a fight over whether a theory that some consider to have high
EO/low BI others consider to have mainly high BS and so should be discarded. These fights, however, when conducted well
are very useful. Contrary to popular opinion: de gustibus very much disputandum
est. In fact, I suspect that it is the main thing worth disputing
scientifically for it is what drives research through its relation to ‘why’
questions. Good taste in ‘why’ questions is worth its weight in Nobel gold.
Last point: what’s all this have to do with science being
the pursuit of truth? Everything. By its
nature, this pursuit must be indirect. Rorty, I think, once said (and I agree)
that ‘true’ functions in science like QED at the end of a proof. It signals
that all the hard work has already been done. We mere mortals must pursue truth
indirectly. How? In large part, by looking for explanations. But explanations
being answers to ‘why’ questions are interest relative (this does not make them irreducibly subjective
however, recall we can and should dispute taste) and so the BI/EO dimension is
critical. Being that it is also subtle and tricky and hard to measure, we need
to be careful to look for it and value it when it arises. The real problem with falsificationism (the
subtle non naïve varieties are generally ignored in real debate) is that it is
so easily deployed to cudgel the interesting and promote the boring. And, as I consider
BI/EO to be very effective routes to the “truth,” falsificationism can have
(and has had) very baleful effects. That was the point I intended to make
before.
[1]
A particularly vivid example of the second is Everett’s observations about
Piraha. His observations are entirely uninteresting as they have zero relevance
to the question he purports to be addressing. However, he gets lots of airtime.
Wasted time in my opinion. I mention this because a whole evening was dedicated
to his claims this past week at the LSA summer institute here at U Michigan
(which aside from this has been really quite enlightening).
[2]
Just look at how excited physicists sound when they think that the Standard
Theory is showing cracks. Whole new physics, whole new questions. The theory is
false, whoopy!
