[Lingtyp] Empirical standards in typology

[Dryer, Matthew]

Volker,

Yes, what you say makes sense, at least in the sense that I now see what you meant given your metatheoretical assumptions. But although our views about what drives languages to be the way they are may be in the same ballpark, we have very different goals. Your characterization is a top-down approach, while mine is a bottom-up (inductive) approach.

You say “For instance, if you claim that there is a suffixing
preference, there is probably some reason for this assumption.” For me, the original basis for believing that there is a suffixing preference derives not from my theoretical assumptions, but from simply observing this pattern among the languages of the world, as many have observed at least as far back as Greenberg. Martin’s raising questions about the reliability of the orthographies used in grammatical descriptions made me realize that the pattern that I and others had observed might be an artifact of unconscious conventions in grammatical description. The study reported in my 2015 ALT talk was originally motivated by my own desire just to know whether it might be an artifact and I went into that study not knowing whether it would provide evidence for a suffixing preference or not. My conclusion that there is a suffixing preference came out of that study and was not based on any assumptions about what might cause such a preference. While I am very interested in explaining crosslinguistic generalizations, I feel that too often linguists put the cart before the horse, offering explanations for generalizations that are not supported by the evidence. Hence the focus of much of my research is simply on testing hypotheses of crosslinguistic generalizations.

I am not suggesting that there is anything wrong with the approach you advocate. But when you propose that one criteria for publishing in LT be "To what extent do you consider the operationalizations valid, with respect to the definition of the tertium
comparationis/comparative concept?", that criterion is based on a methodological assumption not shared by many typologists. Such a criterion would have prevented Joseph Greenberg from publishing in LT, since I believe his methodology was similar to what I have described for myself.

I do agree with much else you have said in your recent emails. I do not consider studies like my 2015 ALT talk to be the last word on the topic, but more like the first word. I think a certain amount of skepticism is better than blind acceptance. I also agree that it is important for authors of studies like mine to make available the raw language data on which their numbers are based. In fact, two months ago, I asked the editor of a journal I had submitted to whether, if the paper was accepted, this information could be made available online. I have already been considering making available such data for many of my previous publications.

Matthew

From: Volker Gast <volker.gast at uni-jena.de<mailto:volker.gast at uni-jena.de>>
Date: Monday, November 20, 2017 at 9:42 PM
To: "Matthew S. Dryer" <dryer at buffalo.edu<mailto:dryer at buffalo.edu>>
Cc: Volker Gast <volker.gast at uni-jena.de<mailto:volker.gast at uni-jena.de>>, William Croft <wcroft at unm.edu<mailto:wcroft at unm.edu>>, Linguistic Typology <lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>>
Subject: Re: [Lingtyp] Empirical standards in typology


Matthew,

This might make sense if one believes in crosslinguistic categories, but I don’t understand what it could mean applied to comparative concepts. It seems to imply that there is a set of
comparative concepts out there that it is our job to discover and identify the properties of. But on my understanding, comparative concepts are not things that exist. Rather, they are
simply notions that are defined for the purposes of a particular typological study. What exists if a continuous multi-dimensional space and the comparative concept is a partially
arbitrary definition of a region within that continuous multi-dimenstional space. From that perspective, I don’t understand what it would mean for the operationalization to be valid.


I think the question is, what exactly do we want to discover? I think we
agree that comparative concepts are a tool, not an epistemological
objective. But a tool for what? My personal view is this (and I suppose a
lot of this is trivial and shared among functional typologists; a more
conrete example follows below): The design of linguistic systems is
restricted in specific ways, most notably by the fact that human language
is used as a means of communication. Now we want to identify such
restrictions (or, more generally, we want to determine the space of
variation), or we have hypotheses concerning such restrictions, based on
what we think about human language (as a system of communication). Such
hypotheses are (intended to be) of a general nature, but they manifest
themselves in particular languages. So we need to find a way of linking
our assumptions about human language per se (with its general design
restrictions) to its specific manifestations in (incommensurable)
particular languistic systems, if we want to test our hypotheses.

In my view the concepts that we use for comparison should be motivated by
our underlying assumptions about human language and its design
restrictions. For instance, if you claim that there is a suffixing
preference, there is probably some reason for this assumption. If your
hypothesis relates to syntagmatic phonology, you will probably use a
comparative concept that is based on notions of syntagmatic phonology,
e.g. 'prosodic word' or 'prosodic phrase' (this example is obviously
inspired by Himmelmann 2014, but no specific implications with respect to
Himmelmann's paper are intended here). Then, you have to find an
operationalization for this -- how can you tell if there is a prosodic
boundary between two segments of speech? This is, basically, a matter of
statistics applied to phonetic data.

So in this (more or less) hypothetical example, you would have to define
prosodic domains, e.g. '(prosodic) word' and '(prosodic) phrase'. These
definitions are based on analyst's concepts - on our, i.e. linguists',
(more or less) shared views of how to analyze streams of speech
syntagmatically. And if I got this right, they would count as comparative
concepts. The operationalization of such concepts is a concrete test
procedure -- for instance, we could set up a threshold length of silence
as an indicator of a prosodic phrase boundary. So a reviewer could take a
stance with respect to the each of the following questions:

* Are the theoretical (comparative?) concepts used, e.g. 'prosodic word',
   'prosodic phrase', well-defined (e.g. relative to commonly accepted
   theories of syntagmatic phonology)? (-> a question of linguistic theory)

* How was the data processed, and has it been submitted in an appropriate
   form to be published? Can the study be replicated? (-> a question of
   reliability)

* Does the way in which (specific instances of) prosodic boundaries are
   identified reasonably reflect the definition that is provided for these
   concepts? (-> a question of validity)

So, for instance, if a given phonological theory assumes that prosodic
phrases are not delimited by pauses, but by boundary tones, a reviewer
could point out that the operationalization of 'prosodic phrase boundary'
as 'pause of a certain length' is not 'valid'. It is in this sense that I
think that operationalizations of comparative concepts can be more or less
valid.

Does that make sense?

Volker


Matthew
From: Lingtyp <lingtyp-bounces at listserv.linguistlist.org<mailto:lingtyp-bounces at listserv.linguistlist.org>> on behalf of Volker Gast <volker.gast at uni-jena.de<mailto:volker.gast at uni-jena.de>>
Date: Sunday, November 19, 2017 at 7:57 PM
To: William Croft <wcroft at unm.edu<mailto:wcroft at unm.edu>>
Cc: Linguistic Typology <lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>>
Subject: Re: [Lingtyp] Empirical standards in typology
Thanks Bill. Note that I didn't say that there is no awareness, or no
discussion, of research methods. What I said is that there are no commonly
accepted standards that we could apply, for instance, when evaluating
journal articles, dissertations or research proposals. I assume that
everyone applies their own, personal standards.
So here are some thoughts about standards in quantitative linguistic
typology:
With regard to coding/annotation, we're dealing with a question of
reliability, which ultimately concerns replicability. Let's assume that
self-annotation cannot be avoided for financial reasons. What about
establishing a standard saying that, for instance, when you submit a
quantitative-typological paper to LT you have to provide the data in such
a way that the coding decisions are made sufficiently transparent for
readers to see if they can go along with the argument? And if you fail to
do so your submission will not even be taken into consideration? This
could include, in addition to the data itself, a description of the coding
process and operational tests for the levels of each variable.
The other questions that have been discussed are mainly questions of
validity (though the distinction has been made using other terms in this
discussion). From my point of view the most important insight from the
distinction between comparative concepts and descriptive categories is
that comparative concepts, our tertia comparationis, are analyst's
("observer-made") concepts, not participant's concepts. That means that we
need to think about operationalizations, as you (Bill) write. So there are
minimally two questions (and I'm not saying anything new here): (i) how
can we define comparative concepts, and (ii) how can they be
operationalized. If you define comparative concepts (e.g. 'word') in terms
of other comparative concepts (e.g. 'vowel harmony'), that doesn't really
help, obviously. What you're really doing is replace one tertium
comparationis with a list of tertia (and if the operationalization is
existential quantification over a set of comparative concepts, I have a
hard time seeing how this can lead to valid results). That's why I
think that functional definitions are better suited as the basis of
crosslinguistic comparison (to the extent that crosslinguistic comparison
situates itself in the functional paradigm, but there seems to be
consensus that this is actually the case). They need to be independent of
the actual operationalizations.
Once you have a proper definition of your comparative concept, you can
think about operationalizations; and obviously, you have to make sure that
the operationalizations, which 'measure out' the individual linguistic
systems, do in fact measure what you think you are measuring; they have to
match the (independent) definition of your tertium comparationis. As we
have seen, it's very hard to establish something like a common sense here.
My view is that minimally, definitions (of tertia/comparative concepts)
and operationalizations should be kept apart, and that authors should be
explicit about both -- which, I'm aware, they often are, as you (Bill)
write, though different terms are used. My point is that this should not
just be regarded as something that is done by 'most' typologists, it
should become a standard. Specifically, the degree of explicitness with
which the operationalizations are explained, and their plausiblity with
respect to the definition of the tertium comparationis (which is
subjective), should be evaluated in the review. This could be implemented
by sending LT-reviewers a list of questions including something like: "Is
the tertium comparationis clearly defined?", "Are the operationalizations
made explicit?", "To what extent do you consider the operationalizations
valid, with respect to the definition of the tertium
comparationis/comparative concept?"
Such criteria could also be integrated into ALT-awards, to encourage young
scholars to apply them.
Best,
Volker
* * *
Prof. V. Gast
http://www.uni-jena.de/~mu65qev
On Sat, 18 Nov 2017, William Croft wrote:

       Dear Volker,
  I think most typologists are aware that (i) defining categories for coding is very hard, especially across languages -- hence all the discussions about comparative concepts on
Lingtyp
(some of which have subsequently been published in some form in Linguistic Typology), of which this discussion of ‘word’ is only the latest; and (ii) that typologists must usually
operationalize those criteria and make the operationalizations as explicit as possible. I think that (i) and (ii) are fairly common practice in typology, despite my previous
comments
about essentialism and methodological opportunism (cherry-picking of criteria).
   On the other hand, your point about mono-annotator annotation is well taken. Nevertheless, the operational factor is this one:
       And I'm not saying that mono-annotator projects are useless, sometimes you just don't have the manpower for multi-annotator projects
  I have recently been working on computational projects that involve annotation, and even there, where there is a lot more large-scale funding than in typology, it is very
expensive to
hire and train annotators, and in the end there are maybe two annotators and a third person acting as adjudicator for a pilot annotation at most. (In fact, most of the effort in
computational linguistics is towards training classifiers to do the annotation automatically on large corpora, and in my small experience those are often worse than mono-annotator
annotations.)
    In typology, there is virtually no funding for any sort of multi-annotator annotation whatsoever. This is especially true for graduate students doing typological dissertations,
but
also for faculty doing typological research. I would guess that many typologists are aware that multi-annotator annotation is preferable, but impractical. But we don’t normally add
a
statement like “We are aware that engaging multiple annotators would improve the reliability of our coding and hence of the results of our crosslinguistic study; but due to lack of
funding, all annotation of the data was performed by the author.” Perhaps we typologists should starting adding such statements.
Best wishes,
Bill
       On Nov 18, 2017, at 6:32 AM, Volker Gast <volker.gast at uni-jena.de<mailto:volker.gast at uni-jena.de>> wrote:
Hi Johanna, even if I could do this diplomatically, I wouldn't, and I think it wouldn't make much sense, as my point is not about specific publications or authors; it's about
common practice (and common practice is reflected in the publications of 'major authorities'). But I think I get your point; so let me be a bit more specific.
A lot of (quantitative) typological work relies on 'coding': Information is extracted from grammars and transformed into a data matrix. Now, it is common practice (and I'm not
excluding myself here) for the coding to be done by the analyst him/herself, and by no one else. But that's considered bad practice in other fields. Ideally, you'd need a team of
annotators coding independently, on the basis of annotation guidelines. The team codes a sample, determines inter-annotator agreement, and adjusts/specifies the annotation
guidelines where necessary. This is done until the inter-annotator agreement is satisfactory. And then you can start with the actual coding. Ideally, the analyst shouldn't be
involved in the coding process, as her annotation decisions might be (subconsciously) influenced by her working hypotheses. (Note that this might be a viable solution to the
question of how comparative concepts can reliably be defined, for a given study; you can just measure how much inter-annotator variation there is; whether or not the
operationalizations make sense is a different question, of course, one of validity. When you use a set of criteria disjunctively, the question is what exactly your
operationalizations are intended to represent.)
Note that I'm not saying that there are no multi-annotator projects in typology (I'm actually involved in two such projects, though one of them is actually a comparative corpus
linguistics project); but as far as I can tell, it is 'basically' comon practice for analysts to code the data themselves. And I'm not saying that mono-annotator projects are
useless, sometimes you just don't have the manpower for multi-annotator projects (and one of the multi-annotator projects I'm involved in was really painful; but it was instructive
to see that even for categories that we thought we had defined rather clearly, inter-annotator agreement was rather low in some cases). But as I said earlier, it would be nice to
have some standards or at least general guidelines for coding typological data. Minimally, I think, the data should be published, along with at least some information on the
operational tests that were applied, even if done by a single annotator.
I hope this clarifies my (too general) remarks in my previous post.
Volker
Am 18.11.2017 um 13:27 schrieb Johanna NICHOLS:
       Volker,
If there's a way to do this diplomatically, could you cite an example or two of  "important publications by major authorities of the field where these criteria are simply not
applied"?   In linguistics we don't have as much technical comment on publications as some other fields do, and maybe we should.  In journals where I see technical comments
sections those comments are refereed, edited, brief, and focused on factual and methodological matters, i.e. about empirical fundamentals and not debate on theoretical
frameworks.
If there's no way to do it diplomatically, never mind.
Johanna
On Sat, Nov 18, 2017 at 12:37 PM, Volker Gast <volker.gast at uni-jena.de<mailto:volker.gast at uni-jena.de>> wrote:
       Matthew -- are you saying that "one cannot rule out disjunctively defined comparative concept" because this is what you did?
       I am not convinced by "disjunctive comparative concepts". Now, that's nothing for you to worry about -- I'm just one reader (actually, audience of your
       ALT/2015-talk) who doesn't buy your conclusions because he doesn't accept your operationalizations.
       But if we want "to talk TO each other (not only PAST each other)", as Martin writes, it would be good to have what other fields call "standards of empirical
       research". We have copied a lot of statistical methods from fields such as the social sciences and biology. I think it would also be beneficial to take a look at
       their standards at the "lower" level -- for instances, wrt how data is gathered, processed and classified, how hypotheses are operationalized, etc., to make sure
       that the results obtained by somebody are also accepted by others (just think of the 5%-threshold for statistical significance, which is just a matter of
       convention).
       I'm aware that this type of remark is annoying for some of you. I teach both corpus linguistics and typology. In corpus linguistics our students deal with very
       basic questions of empirical research -- like the traditional 'quality criteria' -- e.g. (external, internal) validity, objectivity, reliability -- and then, in
       typology, we read important publications by major authorities of the field where these criteria are simply not applied, sometimes the statistics are faulty, and
       students do enquire about this. What can I say? There are no research standards in typology? There is an ongoing discussion about
       "arbitrary/subjective/random/disjunctive comparative concepts" on the Lingtype-list? I'm afraid it wouldn't convince them. What I say is that typology still has
       some way to go to in terms of research methods. There are many non-trivial problems, as we have seen in various discussions on this list, and we should be aware
       that linguistic data is sui generis (for instance, I think we can't adopt just any method/software package from genetics). But we shouldn't use "authority" as a
       criterion in our methodological choices, and the choices shouldn't be made in such a way to legitimize our own research 'ex post'.
       Volker
       Am 18.11.2017 um 07:36 schrieb Dryer, Matthew:
       With respect to Martin’s comment

“It is my impression that such ortho-affixes (= forms written as affixes) are perhaps even more common than “phonologically weak” ortho-affixes, but this is an
empirical question (in his 2015 ALT abstract, Matthew mentions 248 languages with weak affixes, but 308 languages with only affixes of the Tauya type, apparently
confirming my impression).”

I realize that this is a reasonable inference from my abstract, but one often has to simplify things for the purposes of an abstract. My definition of a weak
affix is very narrow and many if not most affixes that are not weak affixes by my narrow criteria can still be shown to be attached phonologically by broader
criteria. Furthermore, I also treat a morpheme as an affix for the purposes of this study if it triggers phonologically conditioned allomorphy in stems it
attaches to and it is clear from Macdonald’s description of Tauya that some of the ortho-affixes Martin mentions do trigger phonologically conditioned allomorphy
in stems they attach to (pp 54, 72, 74, 79).

I counted an affix as weak for the purposes of the study in my 2015 ALT talk only if the description of it in a grammar makes clear that it is nonsyllabic (or has
nonsyllabic allomorphs) or that it exhibits phonologically allomorphy or triggers phonologically conditioned allomorphy in adjacent stems. But in many grammars,
it is only in the discussion of phonology that it becomes clear that a given affix exhibits phonologically conditioned allomorphy or that it triggers
phonologically conditioned allomorphy in adjacent stems. But because I wanted to include a large sample of languages and because it is often unclear from
discussions of phonology whether particular rules apply to particular affixes or stems such affixes combine with, I adopted the procedure of not consulting the
discussions of phonology in classifying ortho-affixes as weak. This made sense for my 2015 ALT talk since I was examining whether there is a suffixing preference
and restricting attention to weak affixes so defined applies equally to prefixes and suffixes. For a different type of typological study, this would have been
inappropriate. This illustrates how comparative concepts are specific to particular typological studies.

Furthermore, there are other factors that I did not examine that are relevant to whether a given ortho-affix is attached phonologically. There may be clear
evidence from allophonic rules, but it is often very unclear from grammatical descriptions whether particular allophonic rules apply to particular ortho-affixes
or stems to which ortho-affixes are attached. And even if the information is there in the grammatical description, it may take a lot of work to see whether they
apply to a particular affix. For example, careful examination of Macdonald’s description of Tauya implies that the benefactive ortho-affix -pe that Martin
mentions is attached phonologically, since she gives examples of phonetic representations of forms containing this morpheme where it takes the form [-be] after
/m/ ([tembe] on page 54).

There might also be evidence from stress, but still be unclear how stress is assigned to forms including ortho-affixes. For example, Tauya has word-final stress,
but it is not clear from Macdonald’s description whether this means that nouns bearing the ortho-affixes that Martin mentions take stress on the ortho-affix.

Some of you may have noticed that what I say here contradicts what I said in my earlier email about comparative concepts needing to be exhaustive. The comparative
concept I used in my 2015 ALT talk was not exhaustive and was in fact disjunctive. Since that seemed appropriate for that study, this suggests that one cannot
rule out disjunctively defined comparative concepts. I sympathize with Martin’s objecting to disjunctive comparative concepts as a way to continue to use
confusing and ambiguous terms and I agree that there is something odd about arbitrary disjunctive comparative concepts, but it is a mistake to simply rule out
disjunctive comparative concepts.

I should note finally that while it is clear that the ortho-affixes that Martin mentions are attached phonologically, they are actually not affixes by either his
criteria or mine since they are clitics that attach to postnominal modifiers. [Martin has written about problems with the use of the term “clitic”. I am in
complete agreement with him about this. But I use the term here and elsewhere in my research (including my upcoming ALT talk on the encliticization preference) as
a label for a comparative concept for grammatical morphemes that are phonologically attached but attach to stems of more than one stem class.]

Matthew
From: Lingtyp <lingtyp-bounces at listserv.linguistlist.org<mailto:lingtyp-bounces at listserv.linguistlist.org>> on behalf of Martin Haspelmath <haspelmath at shh.mpg.de<mailto:haspelmath at shh.mpg.de>>
Date: Thursday, November 16, 2017 at 7:14 PM
To: "lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>" <lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>>
Subject: Re: [Lingtyp] wordhood: bonded vs. bound
Matthew Dryer thinks that wordhood is generally understood by grammar authors in terms of bondedness (= phonological weakness, as shown by nonsyllabicity and
phono-conditioned allomorphy), not in terms of boundness (= inability to occur in isolation).
I don’t know if this is true, but Matthew actually recognizes that grammars often describe grammatical markers as “affixes” even when they do not show the two
“phonological weakness” (or bondedness) features.
For example, Tauya (a language of New Guinea) is said to have (syllabic) case suffixes, but these never show any allomorphy, e.g.
fena’a-ni [woman-ERG]
na-pe [you-BEN]
wate-’usa [house-INESS]
Aresa-nani [Aresa-ALL]
Tauya-sami [Tauya-ABL] (MacDonald 1990: 119-126)
It is my impression that such ortho-affixes (= forms written as affixes) are perhaps even more common than “phonologically weak” ortho-affixes, but this is an
empirical question (in his 2015 ALT abstract, Matthew mentions 248 languages with weak affixes, but 308 languages with only affixes of the Tauya type, apparently
confirming my impression).
For this reason, I have suggested that the stereotypical “affix” notion should perhaps be captured in terms of boundness together with single-root-class
adjacency. Since the Tauya case-markers attach only to nouns, they count as affixes; by contrast, if a bound role marker attaches to both nouns (English “for
children”) and adjectives (“for older children”) as well as to other elements (“for many children”), we do not regard it as an affix (but as a preposition), even
if it is bound (= does not occur in isolation; English "for" does not).
Matthew quite rightly points out that this notion of boundness (which goes back at least to Bloomfield 1933: §10.1) implies that most function words in English
are bound, and in fact most function words in most languages are bound – but this is exactly what we want, I feel, because the best way to define a “function
word” is as a bound element that is not an affix. Linguists often think of function words (or “functional categories”) as defined semantically, but it is actually
very hard to say what is the semantic(-pragmatic) difference between a plural marker and a word like “several”, between a dual marker and the word “two”, between
a past-tense marker and the expression “in the past”, or between a comitative marker and the word “accompany”. It seems to me that these distinctions are best
characterized in terms of boundness, i.e. inability to occur in isolation.
It may be true that occurrence in isolation is a feature of an element that is not easy to elicit from speakers, but in actual language use, there are a very
large number of very short utterances, so at least positive evidence for free status (=non-bound status) is not difficult to obtain.
In any event, it seems clear to me that some key concepts of grammatical typology such as “flag” (= bound role marker on a nominal) and “person index” (= bound
person marker, generally on a verb) require the Bloomfieldian boundness notion, and that these concepts are much easier to work with in typology than the
traditional stereotypical notions of “case”, “adposition”, “agreement marker”, and “pronominal clitic”. (For bound person forms, this was a major lesson of Anna
Siewierska’s 2004 book “Person”.)
Best,
Martin
On 14.11.17 07:02, Dryer, Matthew wrote:
       I have a number of problems with Martin’s proposal:

"Here’s a proposal for defining a notion of “affix”, in such a way that the results do not go too much against our intuitions or stereotypes:

An affix is a bound form that always occurs together with a root of the same root-class and is never separated from the root by a free form or a non-affixal
bound form."

If one examines the notion of “bound” from his 2013 paper, I believe it implies a comparative concept of affix that differs greatly from what most linguists
(at last most non-generative linguists) understand by the term. That’s not a problem for it as a comparative concept, but it is a comparative concept that
differs considerably from the stereotype.

Martin’s definition of “free and “bound” from his 2013 paper is as follows:

"But distinguishing in a general way between bound elements and free elements is quite straightforward, because there is a single criterion: Free forms are
forms that can occur on their own, i.e. in a complete (possibly elliptical) utterance (Bloomfield 1933: 160). This criterion correlates very highly with the
criterion of contrastive use: Only free forms can be used contrastively."

First, I find the notion of complete utterance ambiguous. Does it mean utterances in normal speech or does it include metalinguistic uses (like “What is the
last word in the sentence “Who are you going with”? Answer “with”). I would assume that it does not include such metalinguistic uses. But then many if not
most so-called function words in English would count as bound since they cannot be used as complete utterances. Perhaps other speakers of English would have
different intuitions, but if so that only indicates the lack of clarity in the notion. Furthermore, for many function words in English, I am not sure how to
judge whether they can occur alone as utterances. Many such so-called function words would appear to count as bound by Martin’s definition, though they
would not count as affixes since they lack other properties in his definition of “affix”.

Second, many languages have grammatical morphemes that must occur adjacent to an open class word but which behave as separate words phonologically. These
would all apparently count as affixes by Martin’s definition. Again, I have no problem with this as a comparative concept, only that it means his notion of
affix deviates considerably from the stereotype.

Third, Martin says that his criterion “correlates very highly with the criterion of contrastive use”. But by my intuitions, the ability to occur as complete
utterances does not correlate closely with the criterion of contrastive use, since most so-called function words CAN occur with contrastive use (such as can
in this sentence!), as can some morphemes that are conventionally treated as affixes, like un- in “I’m not happy, I’m UNhappy”. Of course, Martin might
argue that un- is more like so-called function words and less like morphemes conventionally treated as affixes. But the fact remains that un- is easily the
locus of contrast but cannot be used as a complete utterance. I thus see no evidence of a close correlation between the ability to occur as a complete
utterance and the ability to be the locus of contrast.

Finally, it is my experience that languages differ in their conventions regarding what can be a complete utterance. Imagine two closely related languages
that differ in their grammatical rules governing what is a complete utterance. By Martin’s definition, there might be a large number of morphemes that count
as separate words in one language but as affixes in the other language. This strikes me as odd. It seems odd to have a criterion for what is a word and what
is an affix so dependent on the grammatical rules in the language for what constitutes a complete utterance.

Matthew
From: Lingtyp <lingtyp-bounces at listserv.linguistlist.org<mailto:lingtyp-bounces at listserv.linguistlist.org>> on behalf of Martin Haspelmath <haspelmath at shh.mpg.de<mailto:haspelmath at shh.mpg.de>>
Date: Sunday, November 12, 2017 at 10:47 PM
To: "lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>" <lingtyp at listserv.linguistlist.org<mailto:lingtyp at listserv.linguistlist.org>>
Subject: Re: [Lingtyp] wordhood
Mattis List and Balthasar Bickel rightly emphasize that “word” is not a Platonic entity (a natural kind) that exists in advance of language learning or
linguistic analysis – few linguists would disagree here, not even generativists (who otherwise liberally assume natural-kind catgeories).

But I think many linguists still ACT AS IF there were such a natural kind, because the “word” notion is a crucial ingredient to a number of other notions
that linguists use routinely – e.g. “gender”, which is typically defined in terms of “agreement” (which is defined in terms of inflectional marking on
targets; and inflection is defined in terms of “word”).

So is it possible to define a comparative concept ‘word’ that applies to all languages equally, and that accords reasonably with our stereotypes? Note that
I didn’t deny this in my 2011 paper, I just said that nobody had come up with a satisfactory definition (that could be used, for instance, in defining
“gender” or “polysynthesis”). So I’ll be happy to contribute to a discussion on how to make progress on defining “word”.

Larry Hyman notes that other notions like “syllable” and “sentence” are also problematic in that they also “leak”. However, I think it is important to
distinguish two situations of “slipperiness”:

(1) “Leakage” of definitions due to vague defining notions

(2) Incoherence of definitions due to the use of different criteria in different languages

The first can be addressed by tightening the defining notions, but the second is fatal.

To take up Östen Dahl’s example of the “family” notion: In one culture, a family might be said to be a set of minimally three living people consisting of
two adults (regardless of gender) living in a romantic relationship plus all their descendants. In another culture, a family might be defined as a married
couple consisting of a man and a woman plus all their living direct ancestors, all their (great) uncles and (great) aunts, and all the descendants of all of
these.

With two family concepts as different as these, it is obviously not very interesting to ask general cross-cultural questions about “families” (e.g. “How
often do all family members have meals together?”). So the use of different criteria for different cultures is fatal here.

What I find worrying is that linguists often seem to accept incoherent definitions of comparative concepts (this was emphasized especially in my 2015 paper
on defining vs. diagnosing categories). Different diagnostics in different languages would not be fatal if “word” were a Platonic (natural-kind) concept,
but if we are not born with a “word” category, typologists need to use the SAME criteria for all languages.

So here’s a proposal for defining a notion of “simple morphosyntactic word”:

A simple morphosyntactic word is a form that consists of (minimally) a root, plus any affixes.

Here’s a proposal for defining a notion of “affix”, in such a way that the results do not go too much against our intuitions or stereotypes:

An affix is a bound form that always occurs together with a root of the same root-class and is never separated from the root by a free form or a non-affixal
bound form.

These definitions make use of the notions of “root” and “root-class” (defined in Haspelmath 2012) and  “bound (form)” vs. “free (form)” (defined in
Haspelmath 2013). All these show leakage as in (1) above, but they are equally applicable to all languages, so they are not incoherent. (I thank Harald
Hammarström for a helpful discussion that helped me to come up with the above definitions, which I had not envisaged in 2011.)

(What I don’t know at the moment is how to relate “simple morphosyntactic word” to “morphosyntactic word” in general, because I cannot distinguish compounds
from phrases comparatively; and I don’t know what to do with “phonological word”.)

Crucially, the definitions above make use of a number of basic concepts that apply to ALL languages in the SAME way. David Gil’s proposal, to measure “bond
strength” by means of a range of language-particular phenomena, falls short of this requirement (as already hinted by Eitan Grossman). Note that the problem
I have with David’s proposal is not that it provides no categorical contrasts (recall my acceptance of vagueness in (1) above), but that there is no way of
telling which phenomena should count as measuring bond strength.

David’s approach resembles Keenan’s (1976) attempt at defining “subject” (perhaps not by accident, because Ed Keenan was David’s PhD supervisor), but I have
a similar objection to Keenan: If different criteria are used for different languages, how do we know that we are measuring the same phenomenon across
languages? Measuring X by means of Y makes sense only if we know independently that X and Y are very highly correlated. But do we know this, for subjects,
or for bond strength?

Best,
Martin

--
Martin Haspelmath (haspelmath at shh.mpg.de<mailto:haspelmath at shh.mpg.de>)
Max Planck Institute for the Science of Human History
Kahlaische Strasse 10
D-07745 Jena
&
Leipzig University
IPF 141199
Nikolaistrasse 6-10
D-04109 Leipzig
--
Martin Haspelmath (haspelmath at shh.mpg.de<mailto:haspelmath at shh.mpg.de>)
Max Planck Institute for the Science of Human History
Kahlaische Strasse 10
D-07745 Jena
&
Leipzig University
IPF 141199
Nikolaistrasse 6-10
D-04109 Leipzig
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English and American Studies
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