Owning the problem

Written in September 2025 for a private audience. Others have since written more eloquently and publicly about this topic, including Nan and Anastasia.

A peculiar feature of certain global challenges is how few people work full-time on anything. You can have a problem that's demonstrably a big deal, with credible proponents saying it's a big deal, yet an absurdly small number of people actually work on it full-time.

Take, for example, the project of ensuring that terrorists can't use commercially available synthetic DNA to make biological weapons (which I'm currently working full-time on). This sounds important in a self-evident kind of way; it's a publicly stated priority for the White House, UK Cabinet Office, and World Health Organization; and credible NGOs have written many glossy reports on the issue.

And yet, by my count, fewer than twenty people in the world have it as their full-time job to solve this problem.

To be clear, at least a hundred people are Working On It, and thousands Talk About It, but in terms of people who wake up every day thinking, "Today, I'm laser focused on preventing the terrible misuse of synthetic DNA", we're talking about at most two dozen — perhaps even just a handful, if we're strict about the definition of "full-time."

The fact that some of the world's most important problems are many people's side quest and almost nobody's life mission has several unfortunate implications. But these consequences are fairly self-evident to people who've tried to accomplish something very ambitious, so I won't belabor the point. Instead, I'll reflect on why this happens, how you can fix it, and what you'll get in return.

I'll talk about individuals going all-in on a single thing, but these points apply with equal force to the question of organizational strategy, where it's even more rare to see single-minded focus on solving one specific problem.

Why is hardly anyone working full-time on some of the most important problems?

Layered defense, Swiss cheese, and their relatives

In my line of work, a popular argument against narrow scopes is the idea of "layered defense": pandemics won't end by silver bullet, and will instead require a holistic bundle of solutions, including surveillance, countermeasures, public health infrastructure, international coordination, and so on.

I think this is true! And it's especially salient when you have genuine uncertainty about which interventions are best, as we do.

But just because the world needs many things, that doesn't mean that you, personally, have to do all of them. The genuine need for many layers is perfectly compatible with picking one layer, giving it everything you've got, and making it awesome. And if you manage to fix that layer, you can move on and bring your laser focus to the next in line.

TL;DR: The layered defense meme (or Swiss Cheese, or defense-in-depth, or whatever) says something true about what the world needs, but not necessarily about what you should do. More specifically, it doesn't imply that you should work on every single layer of the problem yourself, or even on more than a single layer.

Unfortunate incentives

When people ask, "Why aren't you working on [insert some Legitimately Important Problem]?", it can feel like an allegation that you don't understand the very good arguments for working on the Legitimately Important Problem, or, even worse, that you don't care about it.

I recognize this discomfort, and I think it's normal for people who care about doing good. But there's a much cheaper way to resolve it than dedicating small slices of time to many different issues:

First, you can work on coming to terms with the fact that some people will inevitably express frustration that you aren't helping with their preferred problem, especially if you command significant resources like capital (as a funder), labor (as the director of a large team), or normative influence (as a thought leader). One helpful insight here is that diversifying your efforts to avoid seeming or feeling myopic is a fundamentally losing game. No amount of bet-spreading will cover the entire surface; there will always be an important issue that you're neglecting.

Second, if you really want to demonstrate your understanding and concern for a specific problem: use your words! It's perfectly reasonable to say, "I understand the rationale and care deeply about this Legitimately Important Problem X, but my efforts are more impactful if focused squarely on Legitimately Important Problem Y." I recently wrote a blog post basically making this point about our organization's current priorities, and the few hours it took to write were much more efficient than spending dozens of hours and significant capital on making scattered grants to convey my understanding and concern for the full range of pandemic preparedness priorities.

Of course, many factors spread people thin: the professional incentive to remain open to new opportunities in different spaces; the social desire to have something interesting for any cocktail party conversation; the personal gratification of staying on the steep side of many learning curves; the nagging anxiety of "What if I'm working on the Wrong Thing?".

The bottom line is that focus is rarely the default mode for individuals or teams trying to do good, and there's value to be had in deliberately seeking it out.

What to do?

If you're funding nonprofit work, you have several levers to combat attention sprawl.

Most obviously, narrow your own scope to as few areas as you can muster, taking full ownership of victory in those domains, and come to terms with everything that'll have to go in the "I care about this, and yet I'm not working on it" bucket. (Again, it helps to notice that this bucket will remain full of stuff no matter what you do.)

Secondly, you can encourage, incentivize, and empower others to narrow their scope. This is especially relevant for organizations with multiple funders pulling in different directions — I have a lot of sympathy for leaders trying to satisfy several interests of diverse funders, and you can be tremendously helpful by explicitly encouraging and rewarding focus rather than breadth.

Reflecting with hindsight on the last few years of working in grantmaking, I'd exhibit much greater reluctance to buy small slices of people's time. This is easier said than done — the factors pushing against focus are real and forceful, and buying out senior staff is especially expensive as their opportunity costs far exceed their salary. Still, I've developed a strong intuition that anything less than 0.25 FTE far too often gets rounded to zero in terms of impact, and anything more than 0.75 FTE easily feels like more than 1 FTE.

What you'll get in return

It's obvious that spending your fixed resources on fewer goals lets you move faster, further towards those objectives.

A less widely appreciated benefit of specialization is how it can speed up your learning. This perk — which is counterintuitive given how specialization moves you along the curve of diminishing returns — comes from the fact that focus lets you decisively test hypotheses about tractability.

If you spend a year fixating on a single problem without progress, you have a pretty good signal that your approach might not be tractable. In contrast, token efforts will perennially let you say that you didn't really try — that perhaps, maybe, if you just keep going, it'll eventually work. Crucially, though, you only reap these benefits if you're deliberate about what you're trying to learn and pay attention to it. Less-neglected fields are littered with fruitless interventions that haven't been retired despite talented people sinking dedicated FTE into them.

Of course, there's a tradeoff here — small bets lets you quickly find gems worth scaling. But ruling things out is often more helpful for prioritization than ruling them in. Yes, the world is missing out on great ideas that no one has tried at all, but we're also wasting a ton of resources on perpetually dabbling in things that no one has tried hard enough to realize just won't work.

What to do, specifically

Many super important interventions suffer from being everyone's tenth priority and no one's first.

If you're in a position to allocate resources, try to:

1. Pick a terribly important problem.
2. List the people who get to wake up every day with a singular obsession on solving it.
3. Freak out about how short that list is, relative to the importance of the cause.
4. Help make the list longer.

Thanks for your attention today — and your focus!

Appendix: So you say you want to focus…

… but you might be concerned that:

• What if I'm working on the wrong thing? Odds are that you are! The good news is that you can confidently realize this more quickly by decisively trying things out — although, of course, this whole thing only works if you're actually willing and able to pivot as you learn that you were wrong.
• What if I run out of productive things to do? Although this concern is legitimate, the point of diminishing returns is often well beyond what a single individual or organization can achieve, unless you have the resources to really move the needle in an area. And even then, you should only worry about diminishing returns when you actually hit them; you don't have to preemptively diversify just because you might theoretically exhaust all productive work someday.
• Won't I miss out on the synergies of working on multiple things? There's something to this one as well, but it only works if your interventions actually inform each other (as opposed to merely fitting into some shared category), and the drawbacks of diffused focus may still outweigh the benefits.
• Won't a reputation for myopia cost my credibility? Although "I see she isn't working on X, she must understand/care about it!" often is an invalid inference, it's common enough that it's worth considering how a reputation for monomania might affect your ability to work with certain groups. Exhibiting broad interests will sometimes get you invited to tables you'd quite like a seat at. However! Many non-profit leaders seem wildly miscalibrated about how useful this type of credibility is, sometimes spending so much time acquiring public-relations capital on the conference circuit that they have no time to spend it. I suspect this miscalibration partly owes to the inner discomfort of appearing myopic to your peers (or yourself); in such cases, reflecting on the actual, practical benefits of your brand can be immensely freeing.

— Joshua