[Lingtyp] Empirical standards in typology
Geoffrey Haig
geoffrey.haig at uni-bamberg.de
Mon Nov 20 10:50:21 UTC 2017
Dear All,
A brief comment on the standards for quantitative approaches to
typology: I don't think anyone would disagree that coding-procedures
need to be maximally transparent, explicitly justified, and adequately
illustrated. I also think it's extremely important to minimize
subjective effects in annotation practice - in general more annotators
are better than just one, etc.
But what also needs to be stressed is ensuring the full accessibility
and accountability of the raw data itself - in effect allowing for
replication of the study by other scholars, who are free to opt for,
e.g. different coding decisions (which will likely lead to different
results). That is actually long-term the best way of assessing the
strengths and weaknesses of any coding procedure.
So: if the data are out there, with unrestricted access ("open
science"), then the issue of coding procedures becomes less pivotal.
I would would therefore support recommendations for maximizing data
accountability, accessibility, and replicability, to be a part of
ALT-guidelines, and considered them as criteria for evaluating quality
(e.g. in reviewing publications, or nominations for awards etc.).
best
Geoff
Am 19.11.2017 um 23:33 schrieb Dryer, Matthew:
>
> Volker,
>
> I agree with what you say about the need to have clear operational
> definitions for one’s comparative concepts, but I don’t understand the
> following:
>
> "To what extent do you consider the operationalizations valid, with
> respect to the definition of the tertium comparationis/comparative
> concept?"
>
> 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.
>
> 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 <http://www.uni-jena.de/%7Emu65qev>
>
> 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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> English and American Studies
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--
++++++++++++++++++++++++++++++++++++
Prof. Dr. Geoffrey Haig
Lehrstuhl Allgemeine Sprachwissenschaft
Universität Bamberg
96045 Bamberg
Tel. ++49 (0)951 863 2490
Admin. ++49 (0)951 863 2491
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