Getting from topics to problems

Anthropologist are drawn to topics: peoples, places, things. It’s part of the idiographic focus of our discipline that Boas noticed over a century ago, a fascination with the particular which has also been denounced as exoticizing or orientalizing: we just really really care about Ecuador. It really matters to when the new Methodist church was build in the village square of the place where we did fieldwork. We are the discipline which Leslie White mocked for publishing articles with title likes “An Unusual Prayer Stick From Acoma Pueblo”. Maybe it is because anthropology has always welcomed people who are interested in exploring their own subject positions as women or of color or indigenous, or as indigenous women of color, the Bea Medecines and Katherine Dunhams and Zora Neal Hurstons of our discipline’s past. Maybe it is because the the white guys in our discipline got attracted to it after getting out of the Peace Corp, or being teachers abroad, or otherwise getting hooked up with one particular community. At any rate, we tend to think in topics.

What we are supposed to do is to think in terms of problems: what is the relationship between individual agency and cultural norms? How does the environment affect culture? In what situations does ethnic conflict become violent? We are supposed to think like this because many people whose opinions we care about believe that scientific inquiry should be carried out in this more nomothetic, or generalizing, mindset: lab scientists, for one, whose experiments on rat livers are more driven by the problem ‘how does the body make proteins’ than the topic of ‘rat livers: so fascinating’. Political scientists and sociologist, the members of disciplines adjacent to ours, are also often motivated by this generalizing urge: what similarities can we discern between the Russian, French, and Chinese (Communist) revolutions? What is the relationship between race and quality of treatment in the medical system?

Our tendency to end our topics with periods rather than question marks has more practical outcomes as well. As teachers, we struggle to get out students to understand why the details of Nuer kinship ought to interest them. AAlthough we yearn to be ‘public’ or ‘applied’ when asked ‘what role does religion play in development’ our answer is often ‘They build the Methodist church in the town square in 1952! I fond pictures in the archives!’. Most importantly, the people who fund our dissertation research are, for the most part, interested in its theoretical relevance (‘intellectual merit’ as the NSF puts it) than in the area we study.

How, then, can graduate students learn to turn their topics into problems? How can professors make their ethnography interesting to those uninterested in their topic?

The obvious answer is to make your work ‘theoretically relevant’. In anthropology, this means making the topic you study the perfect place to explore a Big Question in the literature. Topic: Samoa. Problem: how do people use gender roles? Topic: Eighteenth-century Hawai’i. Problem: what is the relationship between structure and agency? Like that.

The problem with this method, of course, is that when you are fascinated by topics rather than problems you 1) don’t know what the Big Questions are because you’ve been busy digging out old photos of churches in the archives instead of reading Cultural Anthropology and 2) you can’t ‘read theory’ because you find it totally boring and not about your topic.

Let me suggest a way out of this problem.

First generalize your topic. What is that thing that you find so fascinating about your topic, and can you find it in other topics? If what really amazes you that they could build this huge gold mine out in the middle of nowhere Amazonia, then perhaps your problem is ‘resource frontiers’. You might even get interested in copper mines in Mongolia because you’re all like ‘hey that’s JUST LIKE what’s happening in the Amazon’. When they built the Methodist church in your town becomes ‘Methodist missions to Latin America’ or perhaps ‘the worldwide spread of Methodism’ or perhaps even something as general as ‘missionization’ or ‘the anthropology of Christianity’.Do you see what’s happened? You now have a generalized and comparative topic rather than one tied to a particular time and place. You have found ethnographic analogies to your field site.

Second find the differences between the particular cases covered by your generalized, comparative topics. In Amazonia they fought the coming of the mine tooth and nail, while in Mongolia they had a large, primarily mutton, barbeque to welcome the mine executives. Hmmm. It looked similar on the surface but now you see some differences.

Third put a question mark on it. The simplest way to do this is what accounts for those differences: Why is mining welcomed in the Amazon but not in Mongolia? Maybe its because the mining operations were different — one had a large environmental impact and the other did not. Maybe it is because rural Mongolians are desperate for cash and people in Amazonia want to stick to subsistence farming (both of these examples are totally made up by the way — sorry all Mongolianists out there).

Fourth, remove proper nouns. Now that you have added the question mark, remove all proper nouns. Go from “Why is mining welcomed in Mongolia but not in the Amazon?” to “Why are resource extraction projects welcomed in some communities but not others?” Or even “what is the relationship between global capital and local communities in the post-9/11 world?”. A fifth optional step, which you can only use for the next 18 months or so, is to add the word ‘assemblage’ to your project title. Congratulations: you have a problem which is ‘intellectually meritorious’.

So: develop comparative scope, look for differences, put a question mark on noted differences, and remove proper nouns. This procedure doesn’t get you in touch with Big Topics (that’s the subject of another blog post) not does it help make one less cynical about ‘theory’, but hopefully it will help topicheads see that even the most abstract theoretical discussions articulate with their own interests if you just follow the intellectual thread that connects them for long enough.

Alex Golub is an associate professor of anthropology at the University of Hawai‘i at Mānoa. His book Leviathans at The Gold Mine has been published by Duke University Press. You can contact him at rex@savageminds.org

30 thoughts on “Getting from topics to problems

  1. rex, are you really interested in Mongolian copper mines!? This is my topic!

    interesting post, I’ve been approaching my pre-dissertation work differently…

  2. bq. A fifth optional step, which you can only use for the next 18 months or so, is to add the word ‘assemblage’ to your project title.

    Don’t you think following through on this step is going to lead to some reviewers throwing you into the “unrealistically ambitious” pile?

  3. MONGOLIAN COPPER MINES FTW!!!!
    I’m interested in what’s happening in Mongolia atm because I study mining, but I don’t have any particular expertise — if you have a reading list please share Marissa :)

    As for that other thing, adding ‘assemblage’ _is_ optional.

  4. Thanks for the post, Rex! I’m currently getting ready to put together my pre-dissertation position papers, so I’ve been struggling with turning my various topical interests (computer-based media, psychological anthropology, Eastern Europe) into research questions…reading this was very helpful. Interestingly, I’ve found that I’ve been having an easier time with the theoretical side of things than the specifics, though…

  5. bq. As for that other thing, adding ‘assemblage’ _is_ optional.
    I didn’t ask because I failed to notice that you mentioned it was optional, I asked because it is the only step of your five which is. I thought some readers might appreciate a discussion of why. But some might appreciate the suspense of not knowing even more, I suppose.

  6. Excuse me, but this was a joke? Right? No hard scientist in his right mind would ever think things through like this. I used to sit in the lab endlessly sequencing DNA, when another grad student asked me what hypothesis I was testing. I told him I had none, that I was just sequencing to my hearts content, and if something would show up I’d find it. Well, months later it did turn out I found something–totally new haplotypes unseen before. Sometimes searching through the particular gains results that have no place in a generalized context, but can add to an overall understanding by the very fact of their being particular. The question marks don’t have to be there. A large part of science is playing in the lab, learning for learning’s sake.
    P.S. those haplotypes I found did get published, and are now part of the big picture.

  7. I must add another two points. Science, no matter the physical or social type, is simply about how the world works. There’s as much “finding how the world works” in literary theory as in physics. True, literary theory may seem impressionistic, but when well done it incorporates the repetoire of human activities while reading into reflections on that very activity. True most physics abstracts the human element, hypothesizes theoretical objects, and is often heavily maths laden; but, it also involves the synthesizing of observations and their correspondence with experimental outcomes. For instance, observations may not correspond with outcomes, as when error creeps into the equation. At times like this theory may be productive in guiding expectations. For instance, I may observe a rainbow, but I cannot locate a rainbow, as it is an optical phenomenon.
    Finally, science, and all sciences, are about interactions between fellow researchers. I needed someone to tell me I had no hypothesis to realize what that actually meant to what I was doing. I also needed lots of people helping me learn in the lab, and helping me with sequencing and aligning sequences. Any sort of research is not a lonely profession/activity. It often and, to my experience, always does involve other people. It is from those generous interactions that the big questions arise, that “topics” become “problems.” What is uncovered through interacting with others is preceisely what you are searching for–by communicating facts, your topic begins to concretize into information that has meaning to other people. Research is always about community, and not a schemata or algorithm to generate a “competent paper.”

  8. Rex, I love the 4 tips. Easily do-able and to be recommended for more than just graduate students in anthropology. They will definitely help increase the “relevance” and “impact” and “visibility” of anth research (apologies for using three such overworked and tired words). Such advice might mean that the 2010 Foreign Policy magazine list of Top 100 Global Thinkers will include more than one anthropologist!
    Barbara Miller

  9. _P.S. those haplotypes I found did get published, and are now part of the big picture._

    Here, Fred, is where your otherwise excellent comments break down. What Thomas Kuhn called normal science depends on exactly the situation you describe. Colleagues agree on a big picture that can then be enriched by small discoveries. Established paradigms for how to do research are communicated through a combination of formal instruction and apprenticeship, which also functions as an initiation into the research community in question.

    Except for odd corners like econometrics or linguistics, the social sciences and humanities are what Kuhn called pre-paradigmatic. A situation worsened by several decades of critique that have dismantled the big pictures that small discoveries could enrich. There are no established paradigms, only endless debates about the possibility of paradigms. Taxpayers and other sources of funding are increasingly skeptical that their money is being spent on work whose value transcends that of relatively harmless hobbies.

    In this sort of context, the process that Rex describes at least draws attention to the possibility of thinking in larger terms. This will not only increase the likelihood of funding, it may add actual value in the form of fresh perspectives. Would that we had established methods like the ones you were trained in and used to find your haplotypes. We don’t. Having given up our grand narratives, we need, as a first step, at least to relate what we do to stories with appeal broader than that of a local history society.

  10. John McCreey> I agree with your assessment that anthropology, like most social sciences, operates in a pre-paradigmatic order. But, most of what we know about ourselves and the world arises from a pre-paradigmatic base. Historians could be said to operate within such a order, and, yet, they seem quite comfortable dealing with the loss of grand narratives (both the epistemological and narrative of emancipation) and continue producing histories knowing all this. I am sure most historians could comfortably justify their work both to fellow researchers, goverment wonks and the public. Historians have navigated the shoals of Hayden White’s history as trope, the pitfalls of cultural history, and managed to accomodate history as narrative. I don’t think anthropology is any the worse, as it has produced some of the most recognizable names in American and European culture, and at a time when the debates over grand narrative had been in full roar. Anthropoogy can produce big-anthropology (the big picture) in the writings of Levi-Strauss or Eric Wolf, or even Marshall Sahlins; while it is also capable of micro-anthropology (the low level, individual focus, local mentalities, a single event) in the writings of Rabinow, or Geertz. If there is a malaise in current anthropology I think it may have to do with something other than debates over the grand narratives, or the fact anthropology is pre-paradigmatic. But I don’t believe focusing research energies on changing “topics” to “problems” is quite the way to go. I think it may ultimately rob anthropology of much of its meaning, much as bowlderizing King Lear in the eighteenth century robbed that play of the force it had in the Elizabethan age. Perhaps, instead of looking to Kuhn for guidance in this, anthropology should look more at Paul Feyerabend as a guide.

  11. One thing you could do is take a look at anthropological archaeology (“Questions are us”). We all work in some small corner of the world, but much of our research is strongly grounded in questions (and in comparisons and theory). Now there are some realms of archaeology where scholars look only at their own regions (think Egyptology, and much of Maya studies), and postmodern archaeologists tend to avoid the kinds of comparative questions you are referring to. But most anthropological archaeologists get good training in research design, theory, and comparison, and much of our academic discourse focuses on questions.

    Could it be that archaeologists might serve as a model for cultural anthropologists? Now that is a heretical question (for both groups of scholars).

  12. Hi, Fred. You are right. If anthropology has a particular strength, it lies in the details of lives studied in all sorts of places that most of those who read the accounts and make use of them in their theorizing never get to go. But as Clifford Geertz observes in the introduction to _Islam Observed_, our insights found in microscopic settings can only be tested for real value in larger conversations.

    How, then, do the historians do it? They situate their topics in relation to the stories that undergird local, national and regional identities of deep, often urgent, interest to large audiences besides themselves. Anthropologists who work in areas with deep area-studies traditions have similar opportunities. Indeed, in the case of my region — the Far East, with particular reference to Taiwan and Japan —the best among us address debates in which, as Geertz forecast, historians, economists, political scientist, sociologists, business people, diplomats and others are already deeply involved.

    In the case of China anthropologists, there is already a rich tradition of interaction between anthropologists and historians that has led to the production of a substantial literature exploring the relevance of anthropological ideas based on observations in the late 19th and 20th centuries to Chinese society and religion in the Tang, Song and earlier dynasties. And, given that China is not only a quarter of humanity but a rising superpower, the odds are that this collaboration will continue into the foreseeable future. It will, perhaps ironically to some, be largely funded by those being studied, or, more precisely, by the political and economic elites who govern the places being studied.

    Do these observations apply to my many friends and colleagues whose research takes them to what remain backwaters in the world system? Not as far as I can see. It used to be that the research they did was seen as a contribution to a broader understanding of humanity as a whole. Seen in that light, it still could be. It could also be of wider interest if seen as contributing substantially to solution of global problems related to ecology, poverty, economic development, healthcare and medicine. Friends involved in applied research still seem to be doing fairly well.

  13. How distressing it is to see what so often passes for the philosophy of science in Political Science — which is to say, a warmed-over mis-mash of Popperian falsification and a Hempelian focus on nomothetic generalization — making its way into Anthropology too. The kinds of precepts that you propose would, I fear, transform Anthropology into something that it decided not to be, as a field, many decades ago: a poor approximation of the techniques of statistical generalization, albeit with more local coloration.

    For my money, the way to get past purely ideographic analysis (a misnomer anyway, but that’s another matter) is to focus more explicitly on site-specific configurations of analytical mechanisms, mechanisms that might recur elsewhere but which won’t generally produce the same effects when they manifest in a different context. Charles Tilly was one of the modern masters of this style of analysis; among the classics, Max Weber stands out. The point here is not to transform the object of one’s fascination into a case of some more general phenomenon; it is to use analytically general specifications of processes to help make sense of what is going on in some specific situation. And you actually signaled that approach, or something like it, with this example:

    “You might even get interested in copper mines in Mongolia because you’re all like ‘hey that’s JUST LIKE what’s happening in the Amazon’.”

    The sense of “just like” here is at the level of a social mechanism, or an abstract account of a process. It’s not what both of these are instances of the same general phenomenon; it is, rather, that a single abstract account of a process sheds light on aspects of both — but one needs site-specific explication in order to really appreciate how the process plays out in practice.

    In sum: don’t reach for facile comparisons at the level of cases; reach for more analytically defensible mechanisms and processes that can be inserted into case-specific accounts. You need proper nouns to construct such accounts, so don’t be too quick to abandon them.

  14. Surely one of the major strengths of anthropology is it’s focus on the particular; moving in the direction of nomothetic explanatory frameworks risks losing that. To echo PTJ, McAdam, Tarrow and Tilly (in their book Dynamics of Contention) offer an alternative framework for generalisation that allows more scope for both the particular and the general.

  15. People who claim a special competence in focusing on the particular should, perhaps, learn to read carefully. Nothing in what either Rex or I is advocating comes close to being a crudely positivist, covering law view of science, and in my particular case I have been a fan of looking closely at particulars for quite a while. The most accessible evidence for you may be my _american ethnologist_ (1995:1) article, “Negotiating with Demons: The Uses of Magical Language.”

    But what Rex knows, and I know, too, has to do with communication, with getting people in other disciplines and, yes, the people who fund research to see value in what we do. A Charles Tilly-style analysis can be a great thing (I, too, am an admirer of Tilly); but the topic has to speak to more than what happened in one small place that people who have never been there simply don’t care about. If you want to make them care, you have to relate it to something general enough to touch their lives or interests as well. The touch can be emotional instead of analytical; but in that case you’d better be a damned good writer, on a par with say Ruth Behar (_Translated Woman_) or Bob Desjarlais (_Shelter Blues_).

    But to write that well, guess what? You have to be able to read closely and come up with something besides clichéd claptrap based on misreadings.

  16. I actually don’t think that this is an example of “clichéd claptrap based on misreadings” as much as the difference in disciplinary contexts and trajectories. Andrew Abbott has a brilliant account of this kind of thing in his book “Chaos of Disciplines.” What sounds like an anthropologist like a call to stop trying to focus exclusively on the particulars of one situation — an option that one simply does not have in many of the other social sciences, because of the dominance of a quasi-statistical notion of knowledge — sounds to a political scientist like a depressingly familiar call for nomothetic knowledge. To us, a focus on particulars is a liberating methodological precept.

    The misreading is probably inevitable, because of where we each come from. Tilly, to anthropologists, plays like a call for general knowledge; to political scientists it plays like a critique of generalization. The word “general” — like, perhaps, the word “theory” — simply means different things in these different contexts. In that case, read my comment simply as a cautionary note, perhaps for an issue of which you are already well aware. A call to consider the general can, I fear, tip all too easily into the kind of ridiculousness that forms the unquestioned backdrop of knowledge-construction in many of the other social sciences. And that’s all I wanted to signal.

  17. Ah, the ‘clearing up misunderstandings’ part of SM — it always seems to happen about 20 comments in. Some of these comments are so wide-ranging that there’s no real way of touching them. Others suggest that I use the example of Charles Tilly to move past a narrow ideographic conception of my research — which I agree with (google “Savage Minds Tilly”). Others seem to think that I am arguing that anthropologists should stop paying attention to particulars altogether, and so on and so forth.

    Just to remind people what I actually wrote: anthropologists think it is a good thing to be able to move from a topic to a problem. A concern for funding and other official apparatuses is one of them — if you don’t believe me look up the NSF’s guidelines for intellectual merit or Wenner-Grenn’s dissertation fieldwork grant. A second reason is that having a wider project is more intellectually fulfilling and gets you in touch with more of the community. Despite anthropology’s ideographic focus, we really are not, say, epigraphers — there are people more ideographic than us, and we like a bit of problem now and then and students have trouble with that sometimes. Thirdly, it was about learning to translate our concerns more broadly to other people who think in different ways about science.

    A couple of comments have argued that I terribly misunderstand science. I can see how people who don’t know me (or the blog) could get that impression. For the record, I do think that most lab work is more about fooling about with the exploration space created by your experimental system (Google “Savage Minds field experimental system”). Some scientists recognize this. Many do not, or misrecognize their work in the lab as a result of the strong cultural emphasis American lab science has on ‘hypotheses’ and ‘the big picture’.

    Pick up any ‘how to write a research proposal’ book and you can see this. Locke’s “Proposals That Work” is a good example — here the emphasis is on deductive methods to help the researcher find a problem in ‘equipoise’ and then conduct an experiment to move it out of equipoise, while the ‘inductive’ qualitative research logics get discussed only because Locke’s editor made him do it.

    So it is obvious that there is a discourse of problem-based science out there — there has always been a camp of anthropologists who even believe this stuff. Whether you agree with its reading of science or not, this is a language anthropologists should try to learn how to speak.

    And of course, trying to think outside your disciplinary box is a good exercise because you just might learn something as well.
    One comment I didn’t get, whose absence surprised me, was the position that anthropology is nothing but ‘theory’ and has gotten away from its ideographic past. I am sympathetic to the critique, and that trying on different conceptions of ‘science’ for size might be a way to help us get back to that detailed ethnography — but only by a process of stimulus diffusion. I’m not the reincarnation of George Murdock.

    Which leads me to Michael Smith’s very intelligent concept about anthropological archaeology, whose mix of empirical focus, thoughtfullness, and comparative scope is really interesting to me. So in fact yes Michael — I think you might be on to something!

  18. And, parenthetically, the procedure that Rex suggests is pretty deductive-nomothetic, especially points 3 and 4. “X (a general phenomenon) causes (i.e., is correlated with to some degree of likelihood) Y (another general phenomenon)” is the basic core of a neopositivist approach to explanation. Sure, one can be nuanced about this. But the core methodology remains. Tilly and Weber, I would suggest, are up to something fundamentally different with their emphasis on causal configurations. For my money, I greatly prefer the latter option as a way of making a topic “speak to more than what happened in one small place that people who have never been there simply don’t care about.”

  19. Prof, we note that you “suggest.” Is there a proof in this pudding? Can you, in other words, show us or point us to something you have written that demonstrates that this suggestion amounts to more than name-dropping and hand-waving?

    This is, of course, a rude question to ask; but it is, I suggest, an essential one. If it turns out that the method in question can only be successfully implemented by a genuine genius like a Weber or Tilly, where does that leave the rest of us?

    One of the virtues of the usual sort of scientific method is that it provides a lot of hack work to be done, experiments to be repeated, that sort of thing. Thus, not every scientist has to be a genius. Can you demonstrate that the same is true of the method you advocate?

  20. I’d argue that Tilly himself provides a pretty good account of how to do this sort of configurational work; there’s a nice web archive of his methodological writings over here: http://professor-murmann.info/index.php/weblog/tilly. The things I myself have written on this are somewhat International Relations-specific, but you might find them useful:

    Jackson, Patrick Thaddeus. 2008. Foregrounding Ontology: Dualism, Monism, and IR Theory. Review of International Studies 34, no. 1: 129-153.

    Jackson, Patrick Thaddeus. 2006. Civilizing the Enemy: German Reconstruction and the Invention of the West. Ann Arbor: University of Michigan Press.

    Also, not by me but very configurational, Nexon, Daniel H. 2009. The Struggle for Power in Early Modern Europe: Religious Conflict, Dynastic Empires, and International Change. Princeton: Princeton University Press.

    Is this methodology as easily routinized as laboratory experiments? No, probably not. But that doesn’t make it any less scientific, IMHO. My extended argument on that score is in my forthcoming book with Routledge called “The Conduct of Inquiry in International Relations,” although the focus there is philosophical rather than operational. Still, such philosophical underlaboring can be useful, especially if the majority of one’s field equates explanation with covering-law hypotheses and simply proceeds from there.

  21. Looks like interesting stuff. But I do believe that we are talking past each other. My concern is not whether configurational research should or should not be labeled science. Neither have I any interest in repeating ancient two-cultures, science versus humanities, nomothetic versus idiographic, Punch-and-Judy shows.

    I do, however, offer two observations.

    1. Michael Jordan has a lot to say about how to play basketball. How many of us can play like that?

    2. Your work is in international relations. The cases in question are nation-states or transnational systems. They and their stories are already of interest to lots of potential readers. Philosophically, there is no reason that studies of obscure villages in Africa or Bolivia couldn’t be conducted in the same way that you study Germany. But how many readers will they attract if not linked to larger issues?

  22. I guess if you wanted to speak the language of Weber (or at least one version of Weber) you could retitle this post “rethinking the value-relevance of your own personal obsession in five easy steps”.

  23. Three brief thoughts.

    1) you’d be surprised how few people find the kind of International Relations topics I do research on to be of interest to them — even if perhaps they ought to be interested because, say, they’re running a postwar reconstruction project in a country they’ve just invaded. But I digress. The broader point here is that it’s a depressing commentary on the state of things if the only way to make case-specific analyses appear of interest to a wider audience is to adopt statistical-comparative ways of framing the project in terms of the impact of general forces/factors (which is how I understand Rex’s suggestions 3 and 4 in the original post). Since I can’t accept that such methodological language in any unique sense accurately mirrors the way that the world is, I can only regard the dominance of that language as part of a cultural project of some kind — and in that way, refusing to use the language is some form of intellectual resistance to the project.

    2) apropos the dead voles post, the problem with the superposition of perspectives is, I think, not in their superposition, but in the often tacit assumption that such superpositions will add up to some coherent whole. That’s clearly encoded into the techniques of large-n statistics, and also into most “qualitative” case-comparison techniques too. All of which is why I prefer the Weberian disclosure of irreducible value-commitments at the heart of methodological perspectives, because that highlights agonism rather than synthesis.

    [It must be fascinating not to have to labor under the burden of "science" in doing one's empirical work. That's not a luxury that we have in my discipline; "scientific status" is often the sine qua non of being allowed to proceed. But you will notice that the only place I have been successful in getting some modest research funding from has not been the NSF, but the NEH. Make of that what you will.]

    3) if I were a basketball player, I certainly wouldn’t delude myself into thinking that I could play just like Jordan. But would I study how Jordan played — not what he said about his playing, but how he actually played — and learn what I could from that? You bet. Would that make me Michael Jordan? Not necessarily; not even likely. But I’ll bet that it would make me a better basketball player.

    And in point of fact, in my forthcoming book on the philosophy of science I actually identify four discrete methodological positions as a way of getting beyond the Punch-and-Judy binary John references (and we both, I infer, find inadequate.) I don’t think that 2-squared is actually the final answer, but at least it’s “progress” in the sense of transformatively operating with existing cultural resources to produce room for something novel. I hope.

  24. Just a couple of stray thoughts -

    In the sociology of knowledge both Weber and Marx will get us to a foregrounding of conflict as the/a substrate of knowledge construction. Mannheim more schematically but still. And of course the critical traditions in cultural studies broadly speaking: feminism, critical race theory, postcolonialism. Point being that to see perspectives as inherently synthesizable (of course they may be, from time to time) or to think that there’s a domain of fact behind perspectives that can be used to reconcile them is already to take a stand against a pretty heavy tradition. For better or worse.

    Jordan was a great basketball player, but oddly enough the things that made him so seem to have also made him worse than useless as a teacher of basketball. He takes his own talent and drive for granted, applies them uncritically and harshly as a standard of judgment, and is unable to take the perspective of others less gifted. As a result he regularly breaks the spirit of lesser players he decides to mentor.

    I have read a ton of yeoman local studies that open with a blast of hot air about their world-historical significance, usually some half-digested fad-theoretical goo that has only the most tenuous relevance to the work. It’s painful and anything we can do to get less of that would be a service to the human race. I wonder if it’s driven less by any actual reader-response effect than by the humanities’ own radical insecurity about the value and durability of our investigative practice. And we’ve done that to ourselves, for better or worse.

  25. I’m a long time reader of SM, but have never commented.

    The mock title ‘rat livers: so fascinating’ made me laugh, out loud, in a very quiet library. Whoops!

    Thanks, Rex, for writing this article, which I have used time and time again trying to tame my thesis into a more coherent argument and away from ‘this shit is interesting (to me)’.

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