How to Choose a Subproblem

An Alignment Research Center (ARC) researcher's practical guide to the skill junior researchers most conspicuously lack: problem-solving strategy. The diagnosis is sharp — olympiad medalists and straight-A MIT grads who have never touched a problem that took more than ten hours flounder when handed a 400-hour research problem, because nobody can write down a 400-step plan. The fix is a fractal discipline of decomposition: peel a 20-hour subproblem off the 400-hour problem, then 1-hour problems off that, choosing each subproblem for the information, skill, or strategic signal it buys.

Key Quotes

"The thing to learn, then, is how to peel the next 20-hour problem off of a 400-hour problem, and then peel 1-hour problems off of that."

The whole essay in one sentence. Decomposition isn't just project management — it's the actual cognitive skill being trained. The framing — "these are important strategic decisions, and making them well requires both practice at the skill and data about the specific problem" — cleanly splits what you can drill in the abstract from what you can only learn on a specific problem.

"The goal for toy problems is to find the very simplest system which has the thing you actually care about."

The author's glass-physics example makes this concrete: instead of window glass (silicon + oxygen + impurities), study a hypothetical one-atom glass. The discipline is identifying which feature of the system carries the phenomenon and discarding everything else. This is TRIZ's abstraction step and Science and Statistics (Box)'s parsimony, applied to choosing what to work on.

"the single most important thing you can do to process information is PUT IT IN A PICTURE"

Fact-processing as its own subproblem type — the information already exists, but it isn't shaped for your brain. The justification is a blunt appeal to hardware: "your brain has a lot more machinery for visual processing than vector calculus."

"Information-theoretically, a yes-no question has at most one bit of information, but a graph can have tons."

The sharpest idea in the piece. The author uses it to correct advice-givers' over-weighting of "actionable information": a high-information move (make a graph) rarely looks actionable in advance, because you can't enumerate the surprises it might surface. It's the greedy-vs-optimal information trade-off from Solving Wordle Using Information Theory, applied to research.

"I call that a quitter attitude!"

The essay's most opinionated move — a direct rebuttal of Jacob Steinhardt's "sort tasks by expected failure probability per unit time." Steinhardt's model assumes one failed subtask kills the whole approach and all intermediate work is worthless. The author counters that major programs (the Manhattan Project, general relativity) are full of insurmountable obstacles surmounted — and that failing early, before you've built muscle and facts, tells you little about whether the idea deserves to live.

"The best measure of whether you can solve a problem is how complete your best plan is. The second best measure is how many plans you have."

The integrals-as-laboratory section is the most useful diagnostic in the essay: difficulty isn't a property of the problem but of your plan of attack. More complete plans, more plans, shorter plans — each a fallible proxy for "can I actually do this," ranked in order of reliability.

"Give up too early and you forgo some scientific knowledge… Give up too late, and you might waste months or years of your career."

The quitting asymmetry, and the essay's answer to it: "the ultimate destroyer of hope: other people." The author credits a fortunate conversation with a random postdoc with saving their grad-school career — a concrete argument that objectivity about your own project is not something you can reliably produce from inside it.

Key Themes

• #concept — Decomposition as the missing skill. Strategy, not raw ability, separates junior from senior researchers. This is The Mundanity of Excellence restated for research: the difference is qualitatively different choices about which subproblem to work, not more hours.
• #pattern — The three moves. Simpler question (start small), simpler system (toy problem / take a limit), and fact-finding ("what the f*** is even going on"). Repeat them fractally, and keep a map of where your subproblem sits in the big picture.
• #concept — Three payoffs, not one. Scientific information, human capital (getting better at the problems you want to solve), and strategic information (learning early whether an approach is doomed). Advice-givers overweight the first; junior researchers overweight the second.
• #tool — The plan of attack as a difficulty gauge. You can't measure a problem's hardness directly, but you can measure how complete, how numerous, and how short your candidate plans are.
• #person — Jacob Steinhardt (referenced and partially rebutted): his fail-fast framework is treated as a useful but over-generalized model that fits ARC's all-or-nothing payoff structure better than most research.

Critical Analysis

The essay earns its confidence through self-deprecating specifics — the Sakai-Sugimoto deep-dive that "never helped with a single thing since," the four-years-later-solved problem that turned out technically ugly and off-track. That willingness to recount personal failures separates it from the usual "advice to young researchers" genre, which runs motivational or abstract.

But the Steinhardt rebuttal has a survivorship problem the author never fully closes. The Manhattan Project and general relativity are the winners — the people who believed in a promising idea and were wrong leave no inspiring anecdotes. The author concedes the point awkwardly: ARC's own agenda-setting is "dominated by Steinhardt-like failure-per-unit-time considerations" because ARC's work is unusually all-or-nothing. That concession reads like the essay talking itself into a corner — the "quitter attitude" critique is aimed at the general case, but the essay's own employer is the exception that needs the fail-fast discipline. The resolution is left implicit: most research has a non-Steinhardtian payoff structure, so don't import a heuristic built for ARC's edge case.

The genuinely under-rated contribution is the reframing of "too easy" versus "too hard." The author insists these failures are not equally bad — a too-hard problem wastes weeks or months, while a too-easy one costs a day and occasionally saves you a month. The corollary ("if there's something which has any chance at all of being important and which you think you could learn in 15 minutes, go and do those fifteen minutes of work") is the single most actionable line in the piece, and the opposite of what perfectionist junior researchers actually do.

The piece's narrowness is a feature, not a bug: it's explicitly aimed at theoretical work (physics, CS, AI alignment), and it says so up front. Readers in empirical or engineering-shaped fields will find the advice transfers only partially — but the decomposition discipline and the payoff taxonomy are domain-agnostic.

Related Pages

• TRIZ — the same meta-claim ("problem-solving has structure you can learn") applied to invention. The three moves are a decomposition toolkit in TRIZ's spirit.
• The Mundanity of Excellence — excellence as qualitatively different choices; here the difference is which subproblem.
• Science and Statistics (Box) — Box's "selective worrying" and the sponsor/critic switch are the same judgment calls as choosing subproblems for actionable information.
• Not-Knowing (Vaughn Tan) — diagnosis before action: the red flags (vague/hard/easy/useless) are a diagnostic-first discipline for research.
• Solving Wordle Using Information Theory — the "one bit vs. a graph" insight is the greedy-vs-optimal information trade-off, applied to research.
• The Usefulness of Useless Knowledge — Flexner defends the curiosity rabbit-holes the author warns to spend honestly.

Sources: raw/how-to-choose-a-subproblem, How to Choose a Subproblem Last updated: 2026-08-21