I have been thinking lately about the following question: What
does comparative/typology (C/T) study contribute to our understanding of FL/UG?
Observe that I am taking it as obvious that GG takes the structure of FL/UG to
be the proper object of study and, as a result, that any linguistic research
project must ultimately be justified by the light it can shed on the fine
structure of this mental organ. So, the question: what does studying C/T bring
to the FL/UG table?
Interestingly, the question will sound silly to many. After all, the general consensus is that one
cannot reasonably study Universal Grammar
without studying the specific Gs of lots of different languages, the more the
better. Many vocal critics of GG complain that GG fails precisely because it
has investigated too narrow a range of languages and has, thereby, been taken
in by many false universals.
Most GGers agree with spirit of this criticism. How so?
Well, the critics accuse GG of being English or Euro centric and GGers tend to reflexively
drop into a defensive crouch by disputing the accuracy of the accusation. The
GG response is that GG has as a matter of fact studied a very wide variety of
languages from different families and eras. In other words, the counterargument
is that critics are wrong because GG is already doing what they demand.
The GG reply is absolutely accurate. However, it obscures a
debatable assumption, one that indicates agreement with the spirit of the
criticism: that only or primarily the study of a wide variety of
typologically diverse languages can ground GG conclusions that aspire to universal relevance. In other words,
both GG and its critics take the intensive study of typology and variation to
be a conceptually necessary part of an empirically successful UG project.
I want to pick at this assumption in what follows. I have nothing against C/T inquiry.[1]
Some good friends engage in it. I enjoy reading it. However, I want to put my
narrow prejudices aside here in order to try and understand exactly what C/T work
teaches us about FL/UG? Is the tacit (apparently widely accepted) assumption
that C/T work is essential for (or at
least, practically indispensible for or very conducive to) uncovering the
structure of FL/UG correct?
Let me not be coy. I actually don’t think it is necessary, though I am ready to believe
that C/T inquiry has been a practical and
useful way of proceeding to investigate FL/UG. To grease the skids of this
argument, let me remind you that most of biology is built on the study of a rather
small number of organisms (e. coli, C. elegans, fruitflies, mice). I have rarely
heard the argument made that one can’t make general claims about the basic
mechanisms of biology because only a very few organisms have been intensively studied.
If this is so for biology, why should the study of FL/UG be any different. Why
should bears be barely (sorry I couldn’t help it) relevant for biologists but
Belarusian be indispensable for linguistics? Is there more to this than just
Greenbergian sentiments (which, we can all agree, should be generally resisted)?
So is C/T work necessary?
I don’t think it is. In fact, I personally believe that POS investigations (and
acquisition studies more generally (though these are often very hard to do
right)) are more directly revealing of FL/UG structure. A POS argument if
correctly deployed (i.e. well grounded empirically) tells us more about what
structure FL/UG must have than
surveys (even wide ones) of different Gs do. Logically, this seems obvious.
Why? Because POS arguments are impossibility arguments (see here)
whereas surveys, even ones that cast a wide linguistic net, are empirically
contingent on the samples surveyed. The problem with POS reasoning is not the
potential payoff or the logic but the difficulty of doing it well. In
particular, it is harder than I would like to always specify the nature of the
relevant PLD (e.g. is only child directed speech relevant? Is PLD degree 0+?). However,
when carefully done (i.e. when we can fix the relevant PLD sufficiently well),
the conclusions of a POS are close to definitive. Not so for cross-linguistic
surveys.[2]
Assume I am right (I know you don’t, but humor me). Nothing
I’ve said gainsays the possibility that C/T inquiry is a very effective way of
studying FL/UG, even if it is not necessary. So, assuming it is an effective
way of studying FL/UG, what exactly does C/T inquiry bring to the FL/UG table?
I can think of three ways that C/T work could illuminate the
structure of FL/UG.
First, C/T inquiry can suggest candidate universals. Second,
C/T investigations can help sharpen our understanding of the extant universals.
Third, it can adumbrate the range of Gish variation, which will constrain the
reach of possible universal principles. Let me discuss each point in turn.
First, C/T work as a source of candidate universals. Though
this is logically possible, as a matter of fact, it’s my impression that this
has not been where plausible candidates have come from. From where I sit (but I
concede that this might be a skewed perspective) most (virtually all?) of the
candidates have come from the intensive study of a pretty small number of
languages. If the list I provided here
is roughly comprehensive, then many, if not most, of these were “discovered”
using a pretty small range of the possible Gs out there. This is indeed often
mooted as a problem for these purported universals. However, as I’ve mentioned
tiresomely before, this critique often rests on a confusion between Chomsky
universals with their Grennbergian eponymous doubles.
Relevantly, many of these candidate universals predate the
age of intensive C/T study (say dating from the late 70s and early 80s). Not
all of them, but quite a few. Indeed, let me (as usual) go a little further:
there have been relatively few new
candidate universals proposed over the last 20 years, despite the continually
increasing investigation of more and more different Gs. That suggests to me
that despite the possibility that many of our universals could have been
inductively discovered by rummaging through myriad different Gs, in fact this
is not what actually took place.[3]
Rather, as in biology, we learned a lot by intensively studying a small number
of Gs and via (sometimes inchoate) POS reasoning, plausibly concluded that what
we found in English is effectively a universal feature of FL/UG. This brings us
to the second way that C/T inquiry is useful. Let’s turn to this now.
The second way that C/T inquiry has contributed to the
understanding of FL/UG is that it has allowed us (i) to further empirically
ground the universals discovered on the basis of a narrow range of studied
languages and, (ii) much more importantly, to refine these universals. So, for example, Ross discovers island
phenomena in languages like English and proposes them as due to the inherent
structure of FL/UG. Chomsky comes along and develops a theory of islands that
proposes that FL/UG computations are bounded (i.e. must take place in bounded
domains) and that apparent long distance dependencies are in fact the products
of smaller successive cyclic dependencies that respect these bounds. C/T work then
comes along and refines this basic idea further. So Rizzi notes that (i) wh-islands
are variable (and multiple WH languages like Romanian shows that there is more
than one way to apparently violate Wh islands) and (ii) Huang suggests that
islands needs to include adjuncts and subjects and (iii) work on the East Asian
languages suggests that we need to distinguish island effects from ECP effects
despite their structural similarity and (iv) studies of in-situ wh languages allows us to investigate the bounding
requirements on overt and covert movement and (v) C/T data from Irish and
Chamorro and French and Spanish provides direct evidence for successive cyclic
movement even absent islands.
There are many other examples of C/T thinking purifying
candidate universals. Another favorite example of mine is how the anaphor
agreement effect (investigated by Rizzi and Woolford) shows that Principle A
cannot be the last word on anaphor binding (see Omer’s discussion here).
This effect strongly argues that anaphor licensing is not just a matter of binding domain size, as the classical GB binding
theory proposes.[4]
So, finding that nominative anaphors cannot be bound in Icelandic changes the
way we should think about the basic form
of the binding theory. In other words, considering how binding operates in a
language with different case and agreement profiles from English has proven to
be very informative about our basic understanding binding principles.[5]
However, though I think this work has been great (and a great
resource at parties to impress friends and family), it is worth noting that the
range of relevant languages needed for the refinements has been relatively
small (what would we do without Icelandic!). This said, C/T work has made apparent the wide range of
apparently different surface phenomena that fall into the same general underlying
patterns (this is especially true of the rich investigations on case/agreement
phenomena). It has also helped refine our understanding by investigating the
properties of languages whose Gs make morpho-syntactically explicit what is
less surface evident in other languages. So for example, the properties of
inverse agreement (and hence defective intervention effects) are easier to
study in languages like Icelandic where one finds overt post verbal nominatives
than it is in English where there is relatively little useful morphology to
track.[6]
The analogue of this work in (other) areas of biology is the use of big fat and
easily manipulated squid axons (rather than dainty, small and smooshy mice
axons) to study neuronal conduction.
Another instance of the same thing comes from the great
benefits of C/T work in identifying languages where UG principles of interest
leave deeper overt footprints than in others (sometimes very very deep (e.g.
inverse control, IMO)). There is no question that the effects of some
principles are hard to find in some languages (e.g. island effects in languages
which don’t tend to move things around much, or binding effects in Malay-2 (see
here)).
And there is no doubt that sometimes languages give us extremely good evidence
of what is largely theoretical inference in others. Thus, as mentioned, the
morphological effects of successive cyclic movement in Irish or Chamorro or
verb inversion in French and Spanish make evident at the surface the successive
cyclic movement that FL/UG infers from, among other things, island effects. So,
there is no question that C/T research has helped ground many FL/UG universals,
and has even provided striking evidence for their truth. However (and maybe this
is the theorist in me talking), it is surprising how much of these refinements
and evidence builds on proposals with a still very narrow C/T basis. What made
the C-agreement data interesting, for example, is that it provided remarkably
clear evidence for something that we already had pretty good indirect evidence
for (e.g. Islands are already pretty good evidence for successive cyclic movement
in a subjacency account). However, I don’t want to downplay the contributions
of C/T work here. It has been instrumental in grounding lots of conclusions
motivated on pretty indirect theoretical grounds, and direct evidence is always
a plus. What I want to emphasize is that more often than not, this additional
evidence has buttressed conclusions reached on theoretical (rather than
inductive) grounds, rather than challenging them.
This leaves the third way that C/T work can be useful: it
may not propose but it can dispose. It can help identify the limits of universalist ambitions. I
actually think that this is much harder to do than is often assumed. I have
recently discussed an (IMO unsuccessful) attempt to do this for Binding Theory
(here
and here),
and I have elsewhere discussed the C/T work on islands and their implications
for a UG theory of bounding (here).
Here too I have argued that standard attempts to discredit universal claims regarding
islands have fallen short and that the (more “suspect”) POS reasoning has
proven far more reliable. So, I don't believe that C/T work has, by and large,
been successful at clearly debunking most of the standard universals.
However, it has been important in identifying the considerable
distance that can lie between a universal underlying principle and its surface
expressions. Individual Gs must map underlying principles to surface forms and
Gs must reflect this possible variation. Consequently, finding relevant
examples thereof sets up interesting acquisition problems (both real time and
logical) to be solved. Or, to say this another way, one potential value of C/T
work is in identifying something to explain given
FL/UG. C/T work can provide the empirical groundwork for studying how FL/UG is
used to build Gs, and this can have the effect of forcing us to revise our
theories of FL/UG.[7] Let me explain.
The working GG conceit is that the LAD uses FL and its UG
principles to acquire Gs on the basis of PLD. To be empirically adequate an
FL/UG must allow for the derivation of different Gs (ones that respect the
observed surface properties). So, one way to study FL/UG is to investigate
differing languages and ask how their Gs (i.e. ones with different surface properties)
could be fixed on the basis of available PLD. On this view, the variation C/T
discovers is not interesting in itself
but is interesting because it empirically identifies an acquisition problem: how
is this variation acquired? And this problem has direct bearing on the
structure of FL/UG. Of course, this does not mean that any variation implies a
difference in FL/UG. There is more to actual acquisition than FL/UG. However,
the problem of understanding how variation arises given FL/UG clearly bear on
what we take to be in FL/UG.[8]
And this is not merely a possibility. Lots of work on
historical change from the mid 1980s onwards can be, and was, seen in this
light (e.g. Lightfoot, Roberts, Berwick and Nyogi). Looking for concomitant
changes in Gs was used to shed light on the structure of FL/UG parameter space.
The variation, in other words, was understood to tell us something about the
internal structure of FL/UG. It is unclear to me how many GGers still believe
in this view of parameters (see here
and here).
However, the logic of using G change to probe the structure of FL/UG is
impeccable. And there is no reason to limit the logic to historical variation.
It can apply just as well to C/T work on synchronically different Gs, closely
related but different dialects, and more.
This said, it is my impression that this is not what most
C/T work actually aspires to anymore, and this is becuase most C/T research is
not understood in the larger context of Plato’s Problem or how Gs are acquired
by LADs in real time. In other words, C/T work is not understood as a first step towards the study FL/UG. This is unfortunate for this is
an obvious way of using C/T results to study the structure of FL/UG. Why then
is this not being done? In fact, why does it not even seem to be on the C/T
research radar?
I have a hunch that will likely displease you. I believe
that many C/T researchers either don’t actually care to study FL/UG and/or they
understand universals in Greenbergian terms. Both are products of the same
conception; the idea that linguistics studies languages, not FL. Given this view, C/T work is what linguists
should do for the simple reason that C/T work investigates languages and that’s
what linguistics studies. We should recognize that this is contrary to the
founding conception of modern linguistics. Chomsky’s big idea was to shift the
focus of study from languages to the
underlying capacity for language (i.e
FL/UG). Languages on this conception are not
the objects of inquiry. FL is. Nor are Greenberg universals what we are
looking for. We are looking for Chomsky universals (i.e. the basic structural
properties of FL). Of course, C/T work might
advance this investigation. But the supposition that it obviously does so needs argumentation. So let’s have some, and to
start the ball rolling let me ask you: how does C/T work illuminate the
structure of FL/UG? What are its greatest successes? Should we expect further
illumination? Given the prevalence of the activity, it should be easy to find
convincing answers to these questions.
[1]
I will treat the study of variation and typological study as effectively the
same things. I also think that historical change falls into the same group. Why
study any of these?
[2]
Aside from the fact that induction over small Ns can be hazardous (and right
now the actual number of Gs surveyed is pretty small given the class of
possible Gs), most languages differ from English in only having a small number
of investigators. Curiously, this was also a problem in early modern biology.
Max Delbruck decreed that everyone would work on e.coli in order to make sure
that the biology research talent did not spread itself too thin. This is also a
problem within a small field like linguistics. It would be nice if as many
people worked on any other language as work on English. But this is impossible.
This is one reason why English appears to be so grammatically exotic; the more
people work on a language the more idiosyncratic it appears to be. This is not
to disparage C/T research, but only to observe the obvious, viz. that
person-power matters.
[3]
Why has the discovery of new universals slowed down (if it has, recall this is
my impression)? One hopeful possibility is that we’ve found more or less all of
them. This has important implications for theoretical work if it is true,
something that I hope to discuss at some future point.
[4]
Though, as everyone knows, the GB binding theory as revised in Knowledge of Language treats the
unacceptability of *John thinks
himself/heself is tall as not a binding effect but an ECP effect. The
anaphor-agreement effect suggests that this too is incorrect, as does the
acceptability of quirky anaphoric subjects in Icelandic.
[6]
One great feature of overt morphology is that it often allows for crisp speaker
acceptability judgments. As this has been syntax’s basic empirical fodder, crisp
judgments rock.
[7]
My colleague Jeff Lidz is a master of this. Take a look at some of his papers.
Omer Preminger’s recent NELS invited address does something similar from a more
analytical perspective. I have other favorite practitioners of this art including
Bob Berwick, Charles Yang, Ken Wexler, Elan Dresher, Janet Fodor, Stephen
Crain, Steve Pinker, and this does not exhaust the list. Though it does exhaust
my powers of immediate short term recall.
[8]
Things are, of course, more complex. FL/UG cannot explain acquisition all by
its lonesome; we also need (at least) a learning theory. Charles Yang and Jeff
Lidz provide good paradigms of how to combine FL/UG and learning theory to
investigate each. I urge you to take a look.
