This
earlier post quoting Rob Chametzky’s typology of linguistic research
generated some interesting discussion, much of it needed in my opinion. I would
like to spend a paragraph or two ruminating (ranting might be more like it) on
the current state of theoretical work
as Rob characterizes it, and in particular, on why there appears to be so
little of it. Before starting, let me reiterate that concentrating on theory is
not intended to impugn the other kinds of research that linguists do. There is
a lot of excellent descriptive and analytic work out there, and three cheers
for that! However, as Peggy pointed out
in the comments section, theory is not generally accorded much of a hearing
unless it comes from Chomsky, and, IMO, even proposals from this quarter are
less well received than they once were. Why?
Peggy offers one very plausible hypothesis: that it is
“easier to evaluate analytical work,” which “adopts some premises, applies them within a domain, and analyzes the
outcome.” How so? Well because “[t]heoretical work involves examination of premises, and
it's much more difficult to convince people that their premises are wrong than
to convince them that such-and-such data can be analyzed within their (perhaps
slightly amended) premises.” Peggy’s observations express Kuhn’s old
observation that “normal science” is, well, the norm, and it generally accepts
and adapts given theoretical conceptions rather than challenges them. So, in
this regard, theory within linguistics is no different from theory anywhere
else.[1]
However,
I am not fully convinced of this. Here’s why. Rob notes that theory itself rests
on meta-theory and meta-theory concerns itself both with general methodological
concerns (simplicity, consistency, relation to other theories etc.) and with
domain specific adequacy conditions. In
the domain of linguistics, the first general methodological concerns have been
made prominent within recent minimalist theory, the hard part being how to
concretize the methodological concerns in the particular setting of linguistics
(e.g. when is a proposal “simpler” or “more elegant” or “less redundant” than
another?). Rob illustrates domain specific meta-theory with Chomsky’s differentiating
theories that are observationally, descriptively and explanatorily adequate.
These meta-theoretical desiderata, especially the third, are where theory
lives. I believe that the field has sometimes forgotten this.[2] And if it has, then the
dearth of theory should be unsurprising. What then are the large
meta-theoretical issues that drive theory?
The
first one, which traces back to what Chomsky likes to call “the earliest days
of Generative Grammar,” is Plato’s problem (PP). The second, is of more recent
vintage, and has been dubbed “Darwin’s Problem” (DP).[3] A theory attains
explanatory adequacy (EA) when it can deduce the attested Gs in combination
with a specification of the PLD. A theory can be EA+ (‘+’ = ‘beyond’) if the
principles the EA theory postulates are ones that did (or at least, plausibly
could have) arisen in humans. The PP, DP duo raise theoretical questions all by
themselves for they pull in opposite directions; PP feeling comfortable with a
richer more linguistically specific FL while DP happier with a poorer less
linguistically specific FL. Reconciling this tension is a worthy theoretical
project all by itself.
Note that
both PP and DP are based on two big, and IMO, hardly contestable facts: viz.
(1) that any human can acquire any language in a pretty short time and in pretty
much the same way regardless of the language at issue when exposed to PLD of
that language, and (2) that human language capacity emerged at some time in the
recentish past from ancestors that were not language endowed the way we are.
These big facts are (two of) the fixed points of our linguistic meta-theory,
and in terms to which theory should be addressed. This meta-theoretical background places demands
both on proposed analyses concerning the structure of particular Gs and on the
structure of FL/UG. And it is precisely these demands that allow for the
evaluation of proposals somewhat independently of whether they are analytically
(in Rob’s sense) sound. In other words, aside from specific familiar linguistic
data (e.g. that ‘flying planes can be dangerous’ is ambiguous) that we use to
evaluate a given proposal, there is also the question of whether a given
proposal can be argued to be acquirable/evolvable. Respect for theory starts with
taking these meta-theoretical demands seriously. IMO, our sensitivity to these
concerns is currently inappropriately low.
Why do I
say this? Here’s some anecdotal evidence for this judgment.
First, I
think that many practitioners of the syntactic arts misperceive what the object
of inquiry is. If asked: “what does linguistics study?” many will answer:
“language.” But language is not the
object of study, at least for generative linguists. The faculty of language
(FL) is. FL in combination with other
cognitive faculties leads to language behavior, utterances, perceptions,
plays, movies, etc. But these products
are not the primary object of inquiry despite the fact that studying language
behavior, both in the wild and in more artificial settings (e.g. acceptability
judgments), has been a good place to find data that bears on the structure of
FL. This noted, the goal of generative grammar has never been to describe or
regiment language (in fact, many generativists, me included, do not believe
that languages are natural kinds and so not appropriated targets of study) but
to describe the fine structure of FL. Now
here’s the kicker: if one thinks that the target of inquiry is language, then
the theoretical considerations that PP and DP lead to will not seem
particularly germane to the enterprise. To address PP and DP we need to advert
to the structure of FL and this involves considerations that go beyond covering
the data that linguists primarily rely on to make their analytical arguments.
Thus, if language replaces FL as the research topic then PP and DP won’t loom
so large with the consequence that theory will seem pointless and, thus, not
surprisingly, it’s pursuit will be undervalued.
I
believe that this shift from FL to language as the cynosure of linguistic
inquiry has gotten greater of late. Here’s some anecdotal evidence. There once
was a time when the first intro chapter of virtually every thesis in syntax
began with a discussion of the logical problem of language acquisition (aka PP)
and ended with a concluding chapter considering what the technically meaty
chapters 2-5 had implied about UG and Plato’s problem. One might argue that
this was mere window dressing and that the formulations and discussions were
very pro forma. To a degree, I would agree with this. However, the required
discussion (even if cursory) pointed to a (tacit) recognition that the details
in the middle were in service of the larger questions driving the field and
this served to legitimate these questions and the theory that lives on them.
Nowadays,
any similar discussion is hard to find. Indeed, I would go further, the very
idea that one’s analytics deserve even cursory consideration in terms of the
more encompassing framework concerns is considered sort of quaint. There’s lots
of concern of how syntax interfaces with semantics or phonology, lot’s of
worries about how structures proposed in language A compare to those in B. But
there is relatively little overt worry about PP or DP.
Here’s a
question for my senior colleagues: How many times have you asked in a public
venue (e.g. at a thesis defense or at a talk), or even over beer, how some
proposal you’ve been talking about (with such and such principles and this and
that parameters) could be acquired? How many of you in teaching about
grammatical variation stop and concentrate on how some rather subtle difference/parameter
one is interested in (e.g. the (purported) difference between English and
Romance wrt extraction out of weak WH islands) could have been acquired/set? I
agree that this is not the only kind
of question worth asking and I agree that an analysis might be valuable even in
the absence of an answer to this kind of question, but in my recent experience,
we act as if this really doesn’t matter at all, which is why such questions are
never raised. Indeed, I suspect that many believe that such questions are
either BS or are more properly addressed to our psycho-ling colleagues or both
(and yes this does suggest a certain kind of unattractive attitude not uncommon
to syntacticians).
I would
add that in my experience linguists tend to be hostile to theoretical
innovation. This is manifest in two ways.
First,
we really don’t like having multiple routes to the same conclusion. In other
fields, it is considered interesting to reach the same end in two different
ways. So there are myriad proofs of the Pythagorean theorem, and all are considered
to be of interest. Why? Why would a novel proof still be publishable (and
published)? Because it is not only interesting that a certain fact is true
(viz. the square of the hypotenuse...) but it is equally (maybe more) interesting
how different concepts link together to demonstrate this.[4] Linking concepts together
is what theory is all about and the reluctance of linguists to prize this kind
of thing betrays a lack of interest in theoretical work.
Second,
the field has a severe “historical bias.” What I mean by this is that we demand
that later proposals surpass in
empirical coverage earlier proposals in order to get a hearing. But why? Why
should a newcomer be required to do better than a senior citizen? In fact,
let’s go one step further, why shouldn’t a newcomer be given some empirical
slack?[5] After all, most of the
proposals we prize have been augmented over time to increase their empirical
range, so why demand of a new proposal that it cover all the ground of the venerable ancestor and more? Isn't this just
a way of making it impossible for new ideas to breathe? And doesn’t this
attitude indicate that what we really care about is that the data points be
covered rather than how they are
covered? And doesn’t this reflect an instrumental conception of theory?
So, in
sum, not only do we often act as if having two ways of thinking about a problem
is intellectually abhorrent, we often act as if theoretical novelty is (or should
be) a punishable offense, novel theory being acceptable only if it brings in
its train wider empirical coverage.
So,
that’s why I think that linguists don’t really prize theory, and that’s too
bad. It’s unfortunate because it reflects the fact that we have turned away from
the foundational questions of the discipline, from the big facts and questions
that, IMO, are the problems of deepest interest. Theory is not the only kind of
inquiry worth doing, but it has its place and we should once again recognize
this. How? Here’s an easy first step: next time you hear a talk or read a
paper, ask yourself how the proposal put forward bears on the structure of FL
and what kind of light it sheds on PP and/or DP, our two great meta-theoretical
questions.
[1]
Interestingly, for this to take place so readily there must be an assumption
that what data are relevant to a
proposal is easy to determine without committing theoretical hostages. I am not
sure that this is always the case. So a chunk of the controversy surrounding
the movement theory of control (something that I am relatively familiar with)
hangs on whether certain observations (e.g. partial control) are reflected in
syntactic representations or not. It is
not clear that this kind of dispute is a purely data dispute however.
[2]
Alex C makes a similar
point in the comments section, though he embroiders it in ways I would not.
[3]
Actually both were big questions posed at the start of the Generative
enterprise. However, as a matter of fact, PP was central to the discussion
since (at least) Aspects while DP
became important only with the advent of the Minimalist Program. There are good
reasons for this (viz. that DP was not really worth discussing until we had
some candidate principles of UG). However, right now, both PP and DP are
important meta-theoretical framework questions.
[4]
Indeed, the route to the conclusion is often more interesting than the
conclusion itself. I recall the following (not verbatim) comment from a
mathematician after the four-color problem was solved via a computer crunching
through all the possibilities: “I guess the problem was not as interesting as
we supposed.”
[5]
A point that Greg Kobele defends in his thesis.
