How to Do Great Work

The standard framing treats curiosity as a fixed trait — either you have it about a subject or you do not. That is mostly wrong, and believing it costs people fields they would have loved.

What actually happens is that curiosity requires enough context to have questions. A subject you know nothing about is not interesting because you cannot see any of its open problems; everything looks equally settled from outside. Push past the first fifty hours and the surface breaks up into things that obviously do not fit, and the interest arrives on its own.

This means the correct response to "I am not interested in X" is often "I do not yet know enough about X to be interested in it." Not always — some subjects really are not for you — but often enough that it is worth testing before you rule a field out.

Taste develops from volume of exposure plus attempted production, and it needs both. Exposure alone produces a critic — someone who can tell you reliably what is wrong with other people’s work and cannot make anything. Production alone produces someone fluent in their own limitations, repeating them confidently.

The mechanism is that you need enough exposure to have an internal standard, and enough production to keep colliding with the gap between the standard and your output. That gap is uncomfortable, and the discomfort is the signal. It is also why the early years of any craft feel bad: your taste arrives years before your ability, and you spend a long stretch able to see exactly how far short you are falling.

The mistake is to interpret that discomfort as evidence you should stop. It is evidence the instrument is working.

Taste is only valuable where it departs from consensus, which is an uncomfortable thing to build a skill around. If your judgements match everyone else’s, they add nothing; the value is entirely in the cases where you think something is wrong and the field does not.

This puts you in a structurally awkward position, because the two explanations for disagreeing with consensus — you are seeing something real, or you are simply wrong — feel identical from inside. There is no internal test that separates them.

What partly resolves it is time and specificity. Vague disagreement with consensus is almost always just taste that has not finished developing. Specific disagreement, where you can say exactly what is wrong and roughly what would be better, is worth acting on even when you turn out to be mistaken — because the specificity means you will learn something either way.

The uncomfortable structural fact about selection is that importance is usually invisible at the moment of choosing. Almost every piece of work now regarded as foundational looked, at the time, like a niche concern pursued by someone with unusual priorities.

This means you cannot select for importance directly. What you can select for are the properties that correlate with it: the problem is real rather than assigned, it has resisted attempts by competent people, the field is not crowded, and solving it would unlock other things rather than just terminating.

That last property is the one I weight most heavily. Problems whose solutions are inputs to other problems compound; problems whose solutions are endpoints do not, however elegant.

Having argued that selection dominates, the obvious risk is over-correcting into permanent evaluation. This is a real and common failure, and it is worse than picking badly, because picking badly at least generates information.

The mechanism is that evaluating options feels productive — it involves reading, thinking, comparing, all recognisably intellectual activity — while producing nothing and, critically, teaching you nothing about the options. You cannot evaluate a research direction from outside it. Most of what you need to know is only available after several months of doing it.

So the correct policy is not careful selection; it is cheap selection followed by fast, honest re-evaluation. Pick the most promising thing in a week, commit hard for three months, and then genuinely allow yourself to abandon it. The commitment is what generates the information; the willingness to abandon is what stops the commitment from becoming a trap.

The highest-yield questions in any field are the ones that sound naive, and they are systematically suppressed because asking them costs status. "Why do we do it this way?" and "what would happen if we just did not?" both risk revealing that you do not know something you are expected to know.

This is why newcomers occasionally produce disproportionate insight and then stop after eighteen months. It is not that they were smarter on arrival. It is that they had not yet learned which questions are socially unavailable, and that ignorance was an asset they subsequently lost.

Keeping it is mostly a matter of deciding that looking uninformed is cheaper than being uninformed. It is, by a large margin, but it does not feel that way in the room.

The skill that separates people who notice things from people who do something with them is the ability to keep a question open without resolving it. Most interesting questions cannot be answered in the sitting in which they occur, and the mind’s strong preference is to close them anyway — with a guess, a dismissal, or a decision to look it up later and then not.

What works for me is a single file of open questions, written as questions, with no obligation to answer any of them. Some sit there for two years. A few resolve suddenly when something unrelated supplies the missing piece, and that only happens because the question was still formulated and available rather than half-forgotten.

The file is also a good diagnostic. If nothing has been added in a month, I have stopped paying attention, and that is worth knowing before it becomes a year.

Everything downstream of selection reduces to one loop: make something, expose it to reality, notice what was wrong, change it. The loop is not sophisticated and the entire difficulty is in running it more times than is comfortable.

Its rate limit is almost always the exposure step. Making is pleasant, revising is tolerable, and showing unfinished work to something that can contradict you is unpleasant enough that people find reasons to defer it. Every deferral costs you a cycle, and cycles are the currency.

So the useful optimisation is not working faster. It is shortening the distance between making and finding out, which usually means showing things earlier and in worse condition than feels appropriate.

Starting and finishing use almost none of the same abilities, and people are rarely good at both. Starting rewards optimism, breadth and tolerance for ambiguity. Finishing rewards narrowing, accepting compromise, and doing unglamorous work on something that is no longer interesting.

The specific difficulty is that the last ten percent is where taste and ambition are least useful and most painful. You can see clearly what the thing should have been, you know you will not get there, and the remaining work is all detail. This is where most projects quietly stop.

The only reliable technique I have found is to decide in advance what finished means, in writing, before the interesting part is over. Deciding later does not work, because by then you are negotiating with someone who wants to start something else.

There is a persistent conflation between work being hard and work being unpleasant, and it causes people to tolerate the wrong things. Hard work is cognitively demanding, frequently frustrating, and satisfying. Unpleasant work is demoralising, and no amount of it makes you better.

A useful diagnostic: after a hard day you are tired and want to continue tomorrow. After an unpleasant day you are tired and want to do anything else. The physical sensation is similar and the direction of the wanting is opposite.

The reason this matters is that people who believe great work requires suffering will keep choosing unpleasant work as evidence of seriousness. It is not evidence of anything except a bad situation.

There is a version of hard problem that only becomes available after years in a field, because it requires enough context to even see it. These are the most valuable problems available and they cannot be accessed early, however ambitious you are.

This reframes the early years usefully. Their purpose is not primarily to produce great work; it is to accumulate the context that makes great problems visible. Work produced along the way is a byproduct and a way of paying for the time.

It also means impatience early on is mostly misdirected. The constraint is not your willingness to attempt something hard. It is that the hard things worth attempting are not yet legible to you, and the only route to legibility is time in the field.

New ideas cluster at boundaries — between fields, between theory and practice, between what a system was designed for and what people actually use it for. The interior of a field is well explored by definition; the edges are where the assumptions have not been checked.

This is partly a supply argument. The population of people who understand two things is much smaller than the population who understand one, so boundary regions are structurally under-explored regardless of how promising they are.

It is also epistemic. Each field carries assumptions that are invisible from inside because everyone shares them. Standing at a boundary makes them visible, because the other field does not share them, and an invisible assumption made visible is frequently an opportunity.

Work that is genuinely new is, by construction, not yet endorsed. That means the period between having the idea and it being taken seriously is spent looking like someone working on something slightly odd, and that period can last years.

Most of the filtering on original work happens here, and it filters on social tolerance rather than on quality. People with good ideas and low tolerance for being unendorsed abandon them for something more legible, and the abandonment feels like a reasonable update rather than a loss of nerve.

The useful adaptation is not to stop caring what people think — very few people manage that and the ones who do are often wrong for unrelated reasons. It is to find a small number of people whose opinion you weight heavily, and to stop weighting the rest much at all.

Every piece of work is made for someone, and if you do not choose who, the default gets chosen for you — usually whoever is most likely to comment. That default is almost never the right audience and it reliably pulls work toward the safe and the legible.

Choosing deliberately is a technical decision, not a marketing one. It determines what you can assume, what needs explaining, what level of rigour is appropriate and what counts as finished. A paper for specialists and an explanation for outsiders are different artifacts even when the underlying content is identical.

The most productive choice I have found is a specific person who is smart, interested and not in your field. It forces you to justify the assumptions you would otherwise skip, and the justification usually improves the thinking rather than only the exposition.

A useful classification: feedback is either about the work, about the presentation, or about the responder. Only the first is directly actionable, and it is the smallest category by a wide margin.

Presentation feedback is real and worth acting on, but it tells you nothing about whether the underlying thing is right. Responder feedback — reactions driven by their preferences, priors or mood — is the largest category and the easiest to mistake for signal, especially when it is confident.

The filter I apply is whether the response would change if the work were presented differently. If yes, it is presentation. If it would change depending on who was looking, it is about them. What survives both tests is the small amount of feedback worth restructuring for.

Given two tasks of equal importance, doing the one that produces visible progress first is usually correct, even when the other is technically more urgent. The visible one refills the tank that pays for the invisible one.

This runs against the instinct to front-load the hardest part, and that instinct is right in one specific case: when the hard part determines whether the project is viable at all. Then you do it first, because the alternative is months of pleasant work on something that cannot succeed.

Outside that case, alternating is better than batching. A long uninterrupted stretch of necessary tedium is where most projects are abandoned, and interleaving it with something that produces a result is not procrastination, it is pacing.

Sustained hard thinking has a duty cycle, and pretending otherwise produces a specific failure: weeks of effort at reduced capacity, generating work that has to be redone. The redone work is invisible in the accounting, which is why overwork appears cheaper than it is.

There is also a substantive reason for rest beyond capacity. A large share of useful insight arrives during deliberate non-work — walking, showering, the gap between sessions — because the mind keeps processing without the constraint of directed attention. Removing all the gaps removes that channel entirely.

The practical version is unglamorous: stop before you are empty, keep at least one day genuinely clear, and treat a walk mid-problem as a technique rather than a break from technique.

Ambition applied at the wrong scope is destructive. Applied to a career it produces useful direction. Applied to a single afternoon it produces paralysis, because no afternoon can carry the weight of a life-scale intention.

The resolution is to hold ambition at the long horizon and standards at the short one. What am I trying to build over ten years is an ambition question. What does this function need to look like is a standards question. Both matter; confusing them is how people end up unable to start.

Practically this means the daily question should be small and answerable. The large question gets revisited a few times a year, deliberately, and then put away again.

The most useful thing the essay does, structurally, is treat a working life as a thing that is constructed rather than a thing that happens. Choices about field, problems, collaborators and standards are design decisions, they interact, and they are revisable.

The consequence is that the relevant unit of evaluation is the trajectory rather than any point on it. A bad year inside a good trajectory is unremarkable. A good year inside a trajectory pointed somewhere you do not want to be is a problem, and it is a problem that feels like success while it is happening.

So the question worth asking periodically is not whether the current work is going well. It is whether it is accumulating into something, and whether that something is what you would choose.