There's a concept in progress studies which I haven't seen discussed, although it's very possibly out there -- if so, apologies + I'd be grateful to know the correct terminology.

Discussions of the importance of an idea or invention use proxies like citation count to measure the impact of the idea -- how influential it has been on later work. (Cf Do Academic Citations Measure the Impact of New Ideas?

I want to argue that the the value[1] "to mankind" of a person or group discovering an idea (or making an invention) is not determined solely by the impact of the idea. There's another factor, and that's how much longer it would have taken to find that idea in the counterfactual world where you remove the discoverer/inventor from the picture. An example to show how these might differ:

Oxygen. Scheele discovered oxygen in 1772, Priestly independently in 1774 (and perhaps Lavoisier in 1775).  The impact of the discovery of oxygen was huge, but the incremental value to mankind of Scheele discovering it was relatively low; in a world without Scheele, Priestly would have discovered it anyway.  

The contribution of a discovery or invention to the overall rate of technological progress is given not by its impact, but by its value. This particularly matters when many people are working in the same area -- a high impact paper by a particular group may actually not have much (incremental) value, because the next group might have been just about to find that idea. Some amount of time that the second group spent will have been duplicative and so wasted.[2]

By contrast, sometimes an idea seems to come out of nowhere, transforming a field; paradigm shifts are more often like this. The best example I know is not a popular one, unfortunately -- when Richard Montague created Montague grammar, it completely transformed/created the nascent field of formal semantics. The tools that Montague were using were from a completely different field (logic), and without Montague I think it's unlikely that they would have been applied for a long time. 

Other high-value examples are the inventions which were not actually made for some time after they were technically possible -- The Knowledge by Dartnell Lewis discusses some. Some such inventions could have been made a century earlier than they actually were; if they had been, that might have resulted in significantly faster technological progress than in our actual history.

One place where distinguishing impact and value matters is in considering how much large research communities contribute to progress. To the degree that the people in such communities are working on the same problems, they are likely racing to find the same ideas, and there will be a lot of duplicated work; accordingly, the value of the (first) discovery of an idea is likely to be relatively small.

  1. ^

    I considered writing marginal value or marginal utility instead of value; marginal thinking is clearly important here, but I'm not a trained economist and I suspect that usage is slightly wrong... .? Incremental value is another option.

  2. ^

    Again this seems somewhat related to deadweight loss, but that's not quite the right term.


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This is an interesting post, and the arguments make sense to me. Upvoted.

I did find one idea which is very popular in economics thinking that I want to push back on:

Some amount of time that the second group spent will have been duplicative and so wasted.

I claim none of the effort spent by the second group is wasted: all of the duplicative effort pays out as reduced time to understand (and therefore use) the discovery. In cases where two groups are very close, that amount of time is basically zero; in cases of multiple discovery it is actually zero. I strongly expect that having multiple groups with a good understanding of a discovery increases the likelihood of successfully getting to downstream discoveries, and I suspect it would disproportionately increase the likelihood of leapfrogging and branching into new areas as the multiple groups look to differentiate themselves.

Separately and not directly related to the post, I claim that situations of multiple discovery are the most valuable events for the study of progress, because they give us n>1 experiments in how much information is required to make the discovery in question. An example of what I mean here is that if the same thing was discovered three independent times, and we look at what each person or group knew when they made the discovery, then:

  • Stuff known by all groups tells us what is necessary
  • The group that knows the least stuff gives us an idea of what is sufficient
  • Stuff that one or more groups was wrong about can be either dismissed as irrelevant, or if another group had it right they could be compared to see what influence that part had on how far they got

The way the second point relates to the first is that I believe the analytical lens which looks at the efficiency of a single discovery - whence the duplicated effort is wasted idea - is fundamentally mistaken. A single discovery doesn't make sense to me as a unit of analysis for this because they are not independent; they depend on the discoveries that came before them and are in turn depended on for later discoveries. If we shift from the abstract discovery level to concrete ones like steps in the chain of producing products, this becomes much more stark: what sense does it make to compare the efficiency of an automated truck in a Uranium mine to the efficiency of an additive in paint manufacturing? In order for the efficiency numbers to make sense we need the context of the process of which they are a part.

Turning at last back to the actual subject of the post - that the value of a discovery by a person or group should be considered in light of the duplicated effort - feels to me like carrying the the same frame of analysis one step farther and applying it to the groups in the research process. If we want to identify which groups we should look to for lessons on progress (which I realize was not identified in the post) then it feels like my intuitions about this point in the opposite direction of yours.

I have seen this kind of analysis before (e.g., this ACX post). There is something to it, but I think in most contexts, the absolute/total “impact” of an idea (using your terminology here) is more important/relevant than the counterfactual/incremental “value.”

There are a few contexts in which the counterfactual/incremental analysis is what you want, but I’m not sure what you learn from that beyond “it’s more valuable to work in neglected areas, rather than crowded ones, all else being equal.” That is a true and important lesson, but not one for which we need to redefine how we measure value.

Re “inventions which were not actually made for some time after they were technically possible” (aka “ideas behind their time”), see some of my recent commentary on this.