A heuristic that we often use when assessing causes is that of neglectedness. If a cause is neglected, then that means that it is not receiving an amount of attention commensurate to it’s seriousness. Given that most causes suffer from diminishing marginal returns on investment, if less has been invested then we should expect there to be especially cost-effective projects still available.

But not all neglectedness is made equal. Some causes are only neglected transiently. That is, they aren’t receiving much attention now, but it’s clear that that will change in the relatively near future. An example is mobile services for the poor. This area has been neglected for a long time because the infrastructure and the handset penetration were not there, but that that is changing. Hence, interest is picking up, and we should expect to see an increasing amount of resources directed there over the coming years. So it’s likely that many potential projects in this area will happen anyway in the next couple of decades.

If a cause is only transiently neglected then the impact of paying attention to it is lesser. If someone else is going to do the work eventually, then by doing it now you have simply brought that time forward. That can be a great thing - getting a malaria vaccine even a year earlier would be fantastic! But it’s even better if we can address a cause that is persistently neglected. In that case you are bringing forward an event which might otherwise require an unusual combination of factors to occur, and therefore probably wouldn’t happen for a long time.

Why might a cause be persistently neglected? One reason can be that there are persistent obstacles to addressing it. For example, many good things can be done by for-profit companies, but there are a number of problems that can persistently obstruct for-profit solutions, for example:

  • The beneficiaries of the project can’t pay for it. For example, attempts to sell high-end electronics to the poor are likely to fail, not because the customers wouldn’t benefit from them, but because they simply can’t afford them.
  • It’s difficult to capture the value created by the project. This can happen because the beneficiaries are not the customers. Anything with large positive externalities has this problem, such as infrastructural projects or provision of public goods.
  • There is a more profitable way to deliver the product to the customers that doesn’t have as much social benefit. For example, one could sell a farmer the ability to get to market by selling them a vehicle, or by building a road. Selling just a vehicle may be more profitable, but the road may benefit many other people as well.

And almost any project can suffer from more general, but still persistent problems, such as:

  • The project requires unusual skills. You might need intimate knowledge of both sub-Saharan Africa and modern financial markets.
  • The project requires unusual knowledge. It is not at all obvious that you can build a cheaper rocket, but Elon Musk had reason to believe that you could.1
  • The benefits of the project are systematically undervalued (e.g. because they accrue in the far future).

Some of these obstacles can be addressed without actually attempting the project! If the reason that nobody is building a cheaper rocket is because they don’t believe that it’s possible, then it may be sufficient to challenge that belief (by argument or example). At that point, if you’ve made a convincing enough case, the problem may become only transiently neglected: now that people realise that it’s possible, somebody else will probably do it soon.2 A lot of academic research falls into this camp - once someone has published a proof of concept, it is only a matter of time before it is implemented.3

So the best kind of project to actually work on, all other things being equal, is one which is both persistently neglected and which cannot be easily made only transiently neglected. This might be because the features that make it possible for you to address it are personal or non-transferrable - unusual skills are a good example of this. So if you can see a project idea which you think relatively few people would even be able to attempt successfully, then it might be a persistently neglected area, and so worthy of extra attention.

  1. Peter Thiel in ‘Zero to One’ refers to these as “secrets”: things that are hard to know, and not widely believed, but are nonetheless true. If you have a secret, it’s likely that you have access to some unusual evidence or theory that can make you particularly suited to address particular problems.

  2. Of course, by the time you’ve demonstrated your principle, you might have enough of a head start that it’s worth pushing on anyway! And it may be a long road to convincing others of unusual beliefs.

  3. Or, for a more industrial example, Elon Musk only produced a white paper about his “Hyperloop” idea, and now there are several teams working on an implementation.