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How to Conduct Research: Cultivating the True Powers of Deliberate Practice

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Research ability is not a talent, but a set of small skills that can be deliberately practiced.

Original Article Title: How to Be Good at Research

Original Article Author: Vivek, AI Analyst

Original Article Translation: MinLi, AI Builder

No one has ever really taught you how to do research. You are handed a desk, a question someone else has picked for you, and a vague instruction to "come up with something new."

As a result, most people reverse-engineer this work through what they can see (such as papers, posts, and announcements). In the end, all they learn is how to "look like" a researcher rather than how to "be" a researcher. True research skill is a stack of small skills, almost all of which can be honed through deliberate practice.

Choose Your Own Problem

Richard Hamming had a habit at Bell Labs that made him quite unpopular during lunchtime. He would ask people sitting next to him what the important problems in their field were and then ask them why they weren't working on those problems. As a result, everyone quickly found excuses to change tables.

This question is uncomfortable because most of us can't provide a good answer. We are not choosing the problems; we are absorbing the problems—from mentors, from announcements released by some big lab last quarter, from papers everyone is citing this week.

The trouble with absorbing problems is that you only hold the conclusions without knowing the reasoning behind them. You know a famous lab cares about a certain direction, but you don't know why, what they expect to find, or what would make them abandon that direction.

You will only realize it a year later when they pivot. Moreover, in a popular problem, you are racing against 1,000 others who started earlier and have more computational power than you.

John Schulman's machine learning research playbook divides this work into two modes. The first, where you read the literature and look for areas to improve. The second, where you pick a result you genuinely care about and then work backward to design an experiment.

He advocates for the second, with its subtle reason being that it fosters originality. A goal you truly care about will take you into territories untouched by any review paper.

As for "taste," people often discuss it as if it were an innate talent. But it actually behaves more like a muscle.

Before running each experiment, predict its outcome; cover the results section of a paper and try to guess the data based solely on the methodology; keep track of which results published this month will still be significant in two years, and then come back to validate your hit rate. One prediction plus one correction, repeated hundreds of times—every good model is trained this way, including the one in your head.

Upgrade Your Input

A shared reading list breeds shared ideas. If your information diet is just the arXiv's top list filtered through group chats, you'll inevitably arrive at the same conclusions as everyone else, rendering those conclusions nearly worthless.

The value of old material is severely underestimated. This field is always replaying its past: the Mixture of Experts (MoE) traces back to 1991, LSTMs to 1997, and backpropagation became mainstream in 1986.

Richard Sutton wrote The Bitter Lesson in 2019 in only a few thousand words, and its predictions for the field's trajectory are more accurate than summaries ten times its length. Claude Shannon gave a talk on creative thinking in 1952, with his first piece of advice being to simplify the problem to near triviality, solve that, and then gradually add back the difficulty.

Just that trick alone can help you break through more walls than any modern production advice could.

Breadth is as important as depth. Explanatory research shamelessly borrows from neuroscience; Evaluation design is just mechanism design in a lab coat; as long as you have a practical understanding of moving memory on a GPU, you can predict which architecture papers are doomed to fail before benchmark results are out; and honest statistics might be the scarcest skill in machine learning, where much of the publicly published "rigor" is just "feel" with error bars.

And one more thing. Read the paper itself, not a post summarizing it. The appendix is where secrets lie, and the "Limitations" section is often the most honest part of the entire document.

Write Everything Down

Paul Graham points out that an idea seems the most mature right before you try to put it into words. But black on white exposes the glossed-over flaws in your brain: untested assumptions, not-so-coherent steps, two quietly contradictory claims.

Feynman's principle is that the first person you must not fool is yourself because you are the easiest person to fool. Writing is the cheapest defense mechanism ever invented.

Darwin went a step further and codified it: Any fact that contradicts his theory is to be immediately written down because he found that his memory deleted inconvenient evidence much faster than it deleted convenient evidence. And so does yours for your track record of failures.

Maintain the habit of journaling: Assumption, Setting, Expectation, Outcome, Updated Perception. Rereading last month's entries will humble you to no end, a level of humility no peer-reviewer can induce.