I was thinking idly about Erdos numbers, and it suddenly struck me that I could easily prove the necessity of a couple of ‘stylised facts'[1] about the associated networks. It’s well-known that the collaboration network for mathematicians contains one big component, traditionally derived by starting with Pal Erdos. The same is true of the network generated by sexual relationships. Although there is no generally agreed starting point here, it is a sobering thought that a relatively short chain would almost certainly connect most of us with both George Bush and Saddam Hussein.
Anyway, the thought struck me that, given a simple two-parameter model, I could prove (at least in a probabilistic sense) not only the existence of a large component but its uniqueness. One parameter would characterise the distribution of the number of connections made by each person, and the other would characterise the bias in favor of endogamy or exogamy. Provided, in an appropriate sense, that these parameters multiplied to a number greater than 1 for some large segment of the population, a network with a starting point in that segment would expand until it contained a substantial portion of the whole population.
It’s easy to see then, that there can’t be two large components (where large means, say, more than 100 members and more than 10 per cent of the relevant population), because the probability that at least one of the possible connections (more than 10 000, by assumption) will be made approaches 1.
I’m recording this not because I think it’s a new discovery, but to raise a general point about research strategy in theoretical problems. The recommended strategy in most fields is to acquaint yourself thoroughly with the literature, then work out what new contribution you might be able to make. My preferred strategy is to begin with only a cursory knowledge of the field in question, work out how I would answer a question of interest and only then consult the literature.
The disadvantage of this approach is that you spend a lot of time reinventing wheels, since most questions of interest have already been answered in one way or another. The advantages, though, are substantial. First, it’s easier to understand something you’ve worked out for yourself than something you’ve read by somebody else. Second, in most research topics, the literature bears the marks of its history. What this means is that the substantive theoretical insights are inextricably mixed with accidental effects. If Professor A, the author of the first big paper in the field, thought that axiom X was crucial and axiom Y was uncontroversial, it’s likely that axiom X will continue to get a lot of attention, whether or not its justified, and that anyone who questions axiom Y will be regarded as ill-informed. If you come to the problem afresh, you may see it differently (not necessarily a good thing if you want to publish lots of articles in journals edited by the students of Professor A, but if you already have tenure this isn’t such a problem).
fn1. This is economist jargon for things we think are true but for which we have no solid evidence
Anyway, I’d welcome anyone pointing me to where my results have been anticipated, as well as any thoughts on research strategy.
John Quiggin 
you have to really clever to reinvent the wheel if you did not know about wheels in the first place.
Pr Q’s post fills me with the pathos of the intellectual under-achiever and reminds me of the scene in the Simpsons where Homer has a job interview:
Marge:: Homer, how’d it go? Did you get the job?
Homer: Nah, they wanted someone good.
you have to really clever to reinvent the wheel if you did not know about wheels in the first place.
Pr Q’s post fills me with the pathos of the intellectual under-achiever and reminds me of the scene in the Simpsons where Homer has a job interview:
Marge:: Homer, how’d it go? Did you get the job?
Homer: Nah, they wanted someone good.
I’ve visited a department where I was told thesis students were instructed to begin their dissertations with a thorough reading of ‘a’ journal article. (The ‘a’ was oddly non-specific). I prefer your approach of beginning with a question , trying to work it out yourself and then going to the literature. Often you understand the literature better when you do this and are less blinkered.
Creativity develops better, as does understanding, if you work from the particular to the general. The general algorithm you suggest follows this precept. Some like Hal Varian have suggested a good mine for problems in economics is the press and media. I also think ideological precepts (This should be true….) can also be a mine for ideas in an evaluative discipline like economics.
Of course with a good fundamental education introspections are more likely to produce something of value.
By the way I read in Sylvia Nasar’s biography of John Nash that Nash set his maths students exam questions that were long-standing unsolved problems in mathematics, such as Fermat’s last theorem. His reasoning: (i) the lack of blinkers suggestion you made and (ii) the idea that the students didn’t start with the presumption that the problems were intrinsically difficult. I don’t think Nash’s approach should be applied too literally.
Although there is no generally agreed starting point here, it is a sobering thought that a relatively short chain would almost certainly connect most of us with both George Bush and Saddam Hussein.
I don’t know about tracking their sexual relationships, but Stanford’s Political Friendster is an interesting project.
John, if by ‘where i’ve been anticipated’ you mean on graph theory not research strategy, you have just described the NK model of stuart kauffman (1993), which computationally simulates the gaint connected component result that was first established by Erdos and Renyi in 1959 and 1960. And interestingly, both of these results were arrived at by your research methodology. Kauffman was studying genetic regulatory networks but refusing to appraoch them via the biochemical route (the preferred axiom A) but rather as cellular automata. Only when he had simulated the result did he uncover the fallow paper by Erdos and Renyi (which is now the new axiom A).
jason, do you have a citation handy?
My colleague William J. Reed (Mathematics, University of Victoria, B.C. Canada) works on these issues. See: “Stochastically Evolving Networks” Physical Review 2003 by Chan, Hughes, Leong & Reed. In PDF format at Reed’s homepage.
John,
I like your research strategy. However from a researcher’s perspective it depends on your current status.
Undergraduates are failed for working this way. Students are generally rewarded for surface learning strategies where they ingest and regurgitate their marker’s favorite literature (the marker won’t give an A to anything they don’t understand… unless it’s a brand name idea).
The strategy works best when you already have a solid reputation in one field and then strike out into another.
Actually I make my students do at least some of their work this way. I set essays/exams in philosophy of mind at USYD where I set them a problem for which there is a big literature, but (having trained them in other literatures) get them to ignore it. They reinvent the wheel, and just ocasionally the hovercraft. But reinventing the wheel is good. At least you really understand the wheel then. And they learn what it is like to invent something: which comes in handy later.
David,
Do you think philosophy teachers are different from those in disciplines like psychology and economics?