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You and Your Research - a talk by Richard Hamming

Modified: Dec 30, 2024Created: Dec 30, 20249 min read

tl;dr

The key to doing significant work is developing the right personal style - a combination of working on important problems, maintaining the confidence to tackle them, and developing effective approaches that fit your personality. This requires both strategic choices (like dedicating time for “great thoughts” and choosing the right environment) and tactical skills (like reframing problems effectively and communicating clearly), all while maintaining a balance between having enough confidence to believe you can do great work and enough humility to keep learning and growing.

In other words, work on the right problem, at the right time, in the right way, with the right style to do great work.

Motivation

  • Hamming felt like a “janitor of science” at Los Alamos: someone who supported the maintenance of the scientific enterprise but did not drive it forward (his “opinion did not matter a great deal”)
    • He wondered, “what’s the difference between the really capable scientists and [himself]”? ⇒ went to Bell Labs to study this
  • Matthew Effect - in science, when you become famous, it’s easy to remain famous. so, it’s necessary to do something outstanding so you become famous. otherwise, your same quality work will be overlooked / forgotten / attributed to others
  • Life advice: try to do significant things (your definition of significant) with your life. It’s more satisfying, he argues.

Common objections people have to pursuing important work and trying to be great/famous

Objection 1: but fame is a matter of luck

  • Hamming’s response: it’s luck (opportunity) and preparation. great scientists create their own luck through relentless work and preparation. they have the inherent ability/energy and drive to work constantly at problems, so when opportunities arise, they are ready to seize them
    • Inherent ability: Feynman’s inherent ability and energy made his success seem inevitable to Hamming
    • Consistent pattern of achievement: Claude Shannon produced great work even before Information Theory (his Master’s thesis)
    • Constant hard work = preparation. As Pasteur says, “luck favors the prepared.”
      • Sir Isaac Newton: if other people thought as hard as he did, they would get the same results
      • Edison: “genius is 99% perspiration and 1% inspiration”
      • At Los Alamos, even when they went hiking in the mountains, they were still talking shop

Objection 2: but you need to have an extremely high IQ to do important work

  • Yes, a common characteristic of great scientists is that they show great deal of ability when young.
  • But many exceptions to this
    • Many great people don’t have extremely high IQs (as measured by normal methods)
    • Newton: wasn’t seen as “exceptional” until he went to Cambridge
    • Einstein: spent 7 years at a Patent Office after his PhD
    • Hamming gives personal example of William G. Pfann (known for development of zone melting)
      • Bill’s own dept didn’t think much of him, but Hamming thought he was doing important work and supported him. ⇒ “It will often be true that your local people cannot see that you are doing great work.”
  • Hamming’s response: traditional measures of intelligence work both ways - they neither rule you out from doing great work, nor guarantee you’ll achieve it. A certain threshold of intellectual capability is necessary but not sufficient.

If you want to do important work, do these things

  • Believe you can do great work. Have confidence in yourself (but not overconfidence)
    • Confidence vs. overconfidence = strong-willed vs. stubborn
    • Examples
      • Claude Shannon
        • Information Theory Breakthrough: When working on random codes, Shannon took an different approach - instead of trying to find one good code, he proved their existence by showing that the average of all possible random codes was good. This meant at least one excellent code had to exist. Taking such an unconventional mathematical approach showed intellectual courage.
        • Chess Playing Style: Shannon’s distinctive style was never playing defense - when attacked, he would counter-attack, letting the game grow increasingly complex. Eventually, he’d pause, think deeply, then make a bold Queen move declaring “I ain’t scared of nothin’” - forcing the game to collapse into either victory or defeat. Hamming copied this style to use when he was stuck / didn’t know what to do next.
  • Make an effort to select for problems that are tractable*, important, and/or have future potential for importance. If you don’t work on important problems, you are (most likely) not going to do important things
    • *tractable = there is a way to attack the problem
  • Whatever you do, try to do it well. Make excellence your standard (for things that matter)
    • Note: recognize you can’t perfect everything. Know where excellence matters most and where “good enough” suffices
  • Work with your door open (literally and figuratively). Allowing others to stop by and chat keeps you connected with reality so you have a better grasp on what’s important and what to work on. Sometimes what appears to be an asset is a defect and vice versa.
    • Example: Institute for Advanced Study (IAS) @ Princeton (door closed) vs. von Neumann (door open)
      • IAS: take in people who have already done something great and give them beautiful offices, dining, and complete freedom. This seemingly ideal working condition is actually isolating and intellectually limiting. Most folks keep working on the thing that made them famous
      • von Neumann: was at IAS but traveled widely and was receptive of new ideas
  • Inverting or reframing the problem (recognizing and addressing the underlying real problem) can sometimes make success more achievable
    • Example: Hamming’s initial task was to solve a 28-order system equation for the Navy using a digital computer. He used a patched-up version of Mill’s method that worked but was inelegant. When faced with writing a government report that he knew would be scrutinized by analog computer users, he realized the significance wasn’t just to solve the equations but to show that digital computers can outperform analog computers at their specialty (diff eq). In response, he developed “Hamming’s method” (a better integration method). tl;dr reframing the problem motivated Hamming to develop a better method, leading to a significant contribution to numerical methods
  • Study your and others’ successes, not failures.
    • What were the elements of their success?
    • Which elements can you adapt and make your own?
    • Example: after Hamming realized John Tukey, a genius colleague his age, worked very, very hard, Hamming did some self reflection. He realized he couldn’t match Tukey’s natural ability, but he could work harder than he currently was.
  • Develop taste for the right problem
    • The “winner” is not the person who works the hardest, but the person who works on the right problem, at the right time, in the right way
    • Example: Hamming set aside Friday afternoons for “great thoughts” - time spent on fundamental questions and bigger-picture implications (e.g. what is the effect of computing on science? what is the nature of software? what should I be doing in computing?)
      • Why Friday afternoons: less likely to be interrupted, thoughts can linger on Sat and Sun
    • Find regular, protected time to stop and thinktoFlashcard
      • What am I really accomplishing here?
        • What is the real problem I am solving?
        • How does this fit into the bigger picture?
      • What is the nature of what you are doing? (underlying principles and patterns)
      • What assumptions am I making?
      • What is the characteristic (essential features, patterns, and requirements) of the job I am doing / field I am in? What skills and mindsets are crucial?
  • Learn new things. Know what is relevant to learn more deeply vs. what is new / interesting but not relevant
  • Tolerate ambiguity. Believe a theory is true enough so you keep working on it, but disbelieve it enough to notice what’s wrong and make the big change to the new theory.
  • Learn how to communicate your work in presentations, written reports, and casual conversations
    • Pay attention to effective lectures/talks you attend. Besides the content, consider the style with which it was presented. Ask yourself:
      • Why were they effective (or not)?
      • What aspects of the speaker can you adapt?
      • Check your opinions with others, and you may find sometimes they don’t agree with you on what’s effective
    • This way, you develop a critical basis to judge your own talks
  • Change does not mean progress, but progress requires change. Most people and institutions resent change
    • You will never find other, better methods if you don’t try other methods. Some of the things you try might make things worse occasionally, but without change, there is no progress

What to avoid

  • The Nobel Prize Winner’s trap - two ways success/fame can actually hinder further important work
    • The mindset trap: winners think they can only work on obviously important problems, paralyzing their productivity
      • ”Acorn to Oaks” Principle: you can’t exclusively work on massive, obviously important, Nobel-Prize-level problems. You should plant acorns (smaller problems—and get good at doing small things well) that have the potential to grow into “mighty oak trees” (important breakthroughs). The key is selecting problems with future potential for importance
    • The practical trap: fame leads to committee appointments and administrative duties that prevent further research work

Other gems

  • Style is everything and is not communicable in words. Right style =
    • Finding your personal approach - methods (on how to work, how much you work, how you communicate your ideas) adapted to your personality and strengths
    • Have a strategic direction - work systematically, identify what’s important vs. interesting
    • High execution quality
  • The onus is on you to demonstrate greatness, and then you’ll get the opportunities and freedom
  • Is it worth it to try to do great (however you define it) work / become a great person? Hamming says he and many other folks he’s spoken with think that “doing something really first-class and knowing you’ve done it is better than anything else they could think of”
    • Perhaps because

      Mastery is the best goal because the rich can’t buy it, the impatient can’t rush it, the privileged can’t inherit it, and nobody can steal it. You can only earn it through hard work. Mastery is the ultimate status.

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