Theory is not a product

Thesis: As an unintended consequence of otherwise desirable changes in the math research enterprise over the last generation, theoretical mathematical research is becoming viewed as if it were a product, and this is not necessarily desirable.

(xxx This version is too unfocused!)

The need for speed?

We are all aware of shifts in the style of conducting research in mathematics and the mathematical sciences over the last generation. One external force has been increased emphasis on interdisciplinary research, prompted by funding agencies and general societal pressure for "relevant" rather than "ivory tower" research. Most of the shifts have been enabled by new technology making collaboration and communication easier and faster -- see e.g. Terence Tao's nice 2010 talk The Future Impact of Internet-Based Technologies on Academia. Though I often pose as a technophobe, I am actually enthusiastic about exploring the possibilities opened up by technology, and was a relatively early adopter of email, LaTeX, arXiv, and even claim (without much evidence except the archaic look) to have been about the 13,000th person with their own web page.

However, the discussions I have seen implicitly assume certain things (speed, in particular) are intrinsically desirable. I will argue on this page that this assumption is based on a partly misleading analogy between "theory" and "product". What do I mean by those words? Well, on a grand scale, developing a 5G phone network or a vaccine for HIV is developing a product. Counterparts in the history of the mathematical sciences, on a similar grand scale, might be Game Theory or Relativity or even the basic setup of math probabability -- "intellectual ideas encapsulated as mathematics". You and I may not work on such a grand scale, but on any scale we should be seeking either a product or an intellectual idea (= "theory"), else what exactly are we doing?

Now I'm quite happy to agree that, for product development, speed is usually desirable, whether for intrinsic human welfare or the demands of a competitive marketplace. But is this self-evident for theory? After all, the proposition

if something is worth doing, then it's worth doing faster
hardly stands scrutiny as a universal generalization; otherwise no-one would spend 3 hours at a baseball game or a concert, or 90 minutes on a good dinner. And eating food reminds us that the proposition
if doing something is worthwhile, then doing more of it is more worthwhile
is equally questionable.

To be as concrete as I can, let us stipulate that over the last generation, largely as a consequence of technological changes,

the time to go from initially thinking about a math project to publication of a write-up (nowadays typically via posting a paper on arXiv) has gone down, and that the volume of mathematical research (number of published pages, per person per year) has gone up.
Is this self-evidently a good thing, as most discussants seem to implicitly assume? Or an indicator of a kind of over-caffeinated culture, as this fridge magnet (on the file cabinet behind my monitor, as I type) suggests?

Three spectra

To avoid getting bogged down in philosophical/aesthetic debate about the purpose of theoretical math research, let me describe three spectra -- where between the two extremes should a research project be?

The product development model vs the traditional mathematics model

Here's what I envisage as typical features of a product development project. And most of these features are equally appropriate for a research lab in the experimental sciences. Now I doubt that anyone explicitly proposes the above as a future model for research in theoretical mathematics. And the decline of the traditional mathematics model -- one individual working alone, not communicating his (usually, his) work until a polished paper appears in a print journal 2 years after the key ideas were worked through -- is deservedly as unregretted as any imperial decline. But this all begs the question -- between these two extremes, what do we want as a replacement "standard model" for conducting theoretical mathematics research? Terence's Tao's article presents a rosy picture of possibilities, which I am all in favor of exploring, but doesn't really suggest any answer more explicit than "technology-enabled collaboration".

Incremental vs transformative

The ESPRC (the U.K. analogue of NSF) asks proposal reviewers to comment on where a research proposal falls on the "incremental to transformative" spectrum, explictly prefering the latter. This raises several issues. Even in an ideal world, could major breakthroughs happen in a vacuum rather than an atmosphere of more routine progress? Can reviewers like you and I really identify proposals that will lead to transformative research? But setting aside such issues and assuming we want institutional structures that promote "transformative research", what model is best for theoretical math? The ESPRC wants timetables for what is to be achieved in the first year, second year etc. This is surely a core aspect of the "product development" model. Does anybody think one can really plan a transformative idea?

Concentration vs dispersion

Amongst a given number of mathematicians working in a given field, would it be better to have more researchers working within each of fewer topics, or fewer researchers working within each of more topics? There can be no right answer, but I surmise that changes over the last generation are pushing toward the "concentration of effort" end of the spectrum.

Here's one example. Traditional annual meetings covering a broad field are now complemented by ad hoc meetings and research institute semesters on ``active topics". Maybe the intention is "here's a new and active topic -- let's publicize it and attract more people to work on it". But in practice it takes a comparatively long time to organize a meeting, while the speed-up of communication means that interesting new techniques or problem topics are quickly seized upon by enterprising researchers. So by the time the actual meeting is held, the effect may be to attract still more people into an already-crowded topic -- the opposite of the original intention!

Collaborative papers and LaTeX

At the level of individual papers there has been a clear shift toward multiple-author papers. Potential advantages are obvious: There seems no intrinsic downside to collaboration. Obviously the arrival of LaTeX and email made collaboration-at-a-distance much easier (previously one had to mail manuscripts or typescripts back and forth). Though as an aside, for those who view math as more a creative art than a science, it should be puzzling that other creative arts (e.g. writing novels) have not seen such increasing technology-enabled collaboration.

LaTeX has made the writing part of writing a paper much easier, and surely it has changed the way one thinks about writing a paper. Pre-LaTeX, the single author would hand-write the mathematical arguments to convince himself he had obtained some substantial result; then make a conscious decision to ``write a paper", which involved starting over with blank paper and deciding how to present the material to other people. Post-LaTeX, it is tempting to write fragments as one thinks about a problem, and have a document grow by accretion. This has two negative consequences. Post-LaTeX papers tend to be longer -- pre-LaTeX one had incentive to choose only the main results to write up, but post-LaTeX it's easier to include everything. And the self-imposed threshold of "novelty and significance" for the content of a paper tends to be lowered, because one is reluctant to discard LaTeX-ed material, and because arXiv provides a venue to post without any threshold constraint.

Here's the main point in this section. I suspect that the combination of collaboration and LaTeX has magnified the negative consequences above, mainly for social reasons. For instance: pruning to the main results might delete one co-author's contributions; different co-authors have different views on what the important material is; one junior co-author might want to expand publication list. All these effects pull toward more and longer papers.

Statistical aside. One could get aggregate time-series data on quantities like average paper length and number of authors, to quantify the changes we are discussing, but it's hard to imagine serious statistical analysis of the causes and effects of these changes, since we're concerned with the "intellectual content" of different papers at different times.


What I have discussed comprises highly selective aspects of the whole mathematical research enterprise, but recall I seek to focus on "unintended consequences". It would be interesting to do a "case study" comparing a few significant new mathematical ideas originating around 1975 with a few others originating around 2005; how did each topic develop over the subsequent 5 years? Here's what I would expect one would find, for 2005 in comparison with 1975. There's nothing bad about this, but it's not clear to me that there's much positive good either. On the other hand, I expect one would also find and the latter seems to me both intrinsically undesirable and having undesirable consequences. For instance, early-career people seeing peers publishing 7 papers a year may be discouraged from spending a year on a single hard problem.

Similarly, the "increased concentration on fewer topics" mentioned earlier (which contributes to the first point above) is neither good nor bad in itself but may have some undesirable consequences, for instance a polarizing effect on young people's careers. A few in each topic may stand out as having made substantial contributions while the others are perceived to have made little marginal contribution; the latter would have achieved more (in substance and in perception) in a more dispersed research environment.

Ultimately one cannot avoid rather philosophical considerations involving the point of theoretical math research, so let me conclude with two.

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