In favor of method diversity by the non-use of giants

I had the impression that, since recognition of [problem] dates back at least to [person from a long time ago], there was a voluminous literature and [statistics to deal with the problem] was a solved problem, so I'm a little troubled that you seem to be trying to invent your own methods and aren't citing much in the way of prior work.

This anonymous critique is saying that I'm not building on top of what there already is but instead re-inventing the wheel, perhaps even a square one. Underlying the criticism is a view of scientific progress as accumulating knowledge over time. We know more stuff now than we used to (but some things we think we know now we still get wrong!) and this is because new scientists don't just start finding out how everything works (the goal of science) from scratch, but instead read what research has already been done and try to build on top of that. At least that is the general idea. However, we know from actual scientific practice that scientists often don't build on top of prior work, perhaps because the body of prior work is already so large that having an overview of it is beyond current human cognitive capacity. Alternatively, because the prior work is often inaccessible, badly structured, not searchable, etc. Othertimes scientists are just lazy. The first problem is in principle unsolvable because improving human cognitive ability/capacity will accelerate the accumulation of knowledge. However, we will (very soon) improve upon the present situation (Shulman & Bostrom, 2014). The second problem is faster to fix, requiring either ubiquitous open access or guerrilla open access. The first option is coming along fast for new material, but won't solve it for old material already locked down by copyright. Probably Big Copyright is going to lobby for extending copyright protection further, which means that even just waiting for copyright to expire is not a legal option. https://www.youtube.com/watch?v=tk862BbjWx4 A delicious example of scientists not building on top of relevant prior works is the concept of construct proliferation (Reeve & Basalik, 2014), which is when we invent a new word/concept to cover the same region in conceptual space as previous concepts already covered. This is itself a redundant copy of the earlier term construct redundancy. This meta-problem is fairly obvious, so my guess is that there is a long list of terms for it, thus illustrating itself. Yet I argue the opposite... Given the above, why would one willingly want to not read the earlier literature/build on top of prior work on a topic before trying to find solutions? There are some possible reasons: One reason is personal. Perhaps one just really likes the experience of finding an interesting problem and coming up with solutions. This is closely related to a couple of concepts: openness to experience, typical intellectual engagement, need for cognition, epistemic curiosity (and more), see (Mussel, 2010) and (Stumm, Hell, & Chamorro-Premuzic, 2011). Incidentally these also show strong concept overlap (this is yet another term to refer to the situation where multiple concepts cover some of the same area in conceptual space, however it is different in that it is explicitly continuous instead of categorical). A career reason to invent new constructs is a desire to make a name for yourself and get a good job. A well-tested way to do that is to introduce a new concept and accompanying questionnaire that others then hopefully use. This can result in hundreds or thousands of citations. For instance, the original paper for need for cognition has 5063 on Scholar since 1982 / 153 per year, the original paper for typical intellectual engagement has 410 citations since 1992 / 18 per year, and that for epistemic curiosity has 156 since 2003 / 13 per year. The later papers do have lower citation counts per year, perhaps indicating some conceptual satiation, but the papers are still way above the norm. To put it another way, since it is clearly unnecessary to read much of the relevant prior work to get published, one may as well skip this. Scientifically speaking, neither of the above two reasons are relevant. The first has more to do with personality disposition towards solving new problems, whereas the second is due, to some degree, to perverse incentives. Exploratory bridge building Are there any good scientific reasons to sometimes start from scratch? I think so. Think of it this way: Many scientific questions can be approached in multiple ways. We can build a large analogy out of that idea. Imagine a many-dimensional space where some regions are impassable or slow to pass, and where there are one or more regions or points from which useful resources can be extracted. We, the bridge engineers, start somewhere in this space (all in the same place) and have to find resources but we don't know exactly where they will be found, so we don't know exactly which directions to move in. Furthermore, imagine that we can build bridges (vectors) in this space by adding them together and that we can only move on the bridges (or in them). This means that one can now travel in a particular direction, at least slowly. If the resources are far away from the beginning position, it is easy to see that one could never reach them without adding vectors together. This forms the basis of the general preference for building on prior work. How do we know which direction to build bridges in if we don't know where the resources are? We can expand the analogy further by saying that no one has the ability to see further than a short distance. Instead, what engineers have is a noisy measure of how close their current position is to the nearest resource. Noisy here meaning that they are only roughly correct, to varying degrees and with different biases. Sometimes what appears to be a good general direction towards a resource to many engineers ends up in a resource poor dead end, i.e. all directions to move closer to nearby resources requires going thru impassable or difficult to pass regions (say, regions where the price of building bridges are very high). Those familiar with evolutionary biology should now see where I'm going with this. We can say that approaches to answers in science can end up in local maximums in the science fitness landscape. When this happens, one has to go back and move in a new direction somewhere. Still, this leaves us with the question of how far we should move back. Often it may be necessary to go back only some of the way and start a new branch of the same root bridge from that point. Sometimes, however, a very early part of the bridge moved into a regional that can only result in slow progress or even a dead-end. When this happens, one has to start over entirely. Decision making Because all engineers are short sighted, it is impossible for them to know when it is time to start over. Worse than that, engineers have a kind of tunnel vision such that when they have once traveled out on given bridge from their homeland, they will be less capable of spotting good directions to build other root bridges from. In other words, once one has learned of a particular approach to a problem, it can be difficult to go "back to basics" and start over with new ideas. One needs a pair of fresh eyes. The only way to do this is to get an engineer who has never been to this space before, avoid informing him of the already built bridges and let him choose where to build his first bridge and let him work on it for some time to see if he ends up in a dead end or a previously unknown resource rich area. Even if the engineers have already found one good resource region, they might wonder whether there are more. Finding more resources probably requires moving in a new direction from the beginning or at least from an early part of the bridge. Balance It is clear that as a large team project neither extreme solution is optimal: 1) always building on prior work, or 2) never building on prior work. Instead, some balance must be found where some, probably most, engineers are dedicated to building on top of the fairly recent prior work, but some engineers should try to backtrack and see if they can find a better route to a currently known resource area or identify new regions. Who should start new bridges? We may posit that the engineers vary in their psychological attributes in ways that have an effect on their efficiency of building on prior bridges or starting their own root bridges/branches. In that case, engineers who are particularly good at spotting new directions and working on their own bridge alone would be good for the role of pioneer/Rambo engineers. Even if there are no differences between the efficiency of the engineers re. building new branches/roots or building on top of prior work, if only a few engineers are inclined to working alone perhaps finding new resources (reason #1), the optimal team strategy is where most engineers build on fairly recent prior work but some don't. Meta-remarks Given the abstractness of the space bridge engineer analogy, one should probably do a visualization, or maybe even a small computer game. The last is beyond my coding ability at the time being and the first requires more time than I have.

References

Mussel, P. (2010). Epistemic curiosity and related constructs: Lacking evidence of discriminant validity. Personality and Individual Differences, 49(5), 506–510. http://doi.org/10.1016/j.paid.2010.05.014 Reeve, C. L., & Basalik, D. (2014). Is health literacy an example of construct proliferation? A conceptual and empirical evaluation of its redundancy with general cognitive ability. Intelligence, 44, 93–102. http://doi.org/10.1016/j.intell.2014.03.004 Shulman, C., & Bostrom, N. (2014). Embryo Selection for Cognitive Enhancement: Curiosity or Game-changer? Global Policy, 5(1), 85–92. http://doi.org/10.1111/1758-5899.12123 Stumm, S. von, Hell, B., & Chamorro-Premuzic, T. (2011). The Hungry Mind Intellectual Curiosity Is the Third Pillar of Academic Performance. Perspectives on Psychological Science, 6(6), 574–588. http://doi.org/10.1177/1745691611421204