9 ms·

You and Your Research (1986)

186 points by ftxbro 4y ago

jzelinskie 4y ago
Here's a recording from '95 entitled the same: https://www.youtube.com/watch?v=a1zDuOPkMSw https://www.youtube.com/watch?v=a1zDuOPkMSw I also highly recommend reading the Stripe Press book also with the same name: https://www.amazon.com/dp/1732265178 https://www.amazon.com/dp/1732265178
- netcraft 4y ago
  I came to also recommend the book. The last half is about specific engineering topics, but the first half is packed with great ideas and thoughts that anyone will find valuable. Its also a beautiful and well made book.
- teddyh 4y ago
  Better video quality, same source material: https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR89bl7hTOS3F3wuoGj7id3Xy&index=32#t=22s https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR...
shae 4y ago
Get the book! It's packed with great content.
teddyh 4y ago
On video: https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR89bl7hTOS3F3wuoGj7id3Xy&index=32#t=22s https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR...
reachtarunhere 4y ago
One of the points of the talk is emphasis on working on "important" problems. It does make sense to not work on incremental things for merely publications so it is definitely good advice. However once you decide to do so what is "important" becomes a difficult question. I like this article from Daniel Lemire which explores this further https://lemire.me/blog/2010/03/22/so-you-know-whats-important/ https://lemire.me/blog/2010/03/22/so-you-know-whats-importan...
- Swizec 4y ago
  The way I’ve always interpreted this is that if even you don’t think it’s important, why are you doing it? Sure you can’t accurately predict what will and won’t be important long term, but you should think your work is important. Whether you’re right or wrong time will tell.
  - reachtarunhere 4y ago
    Yes my interpretation is that this is more an advice on what not to do - frivolous stuff you don't believe in
- marcosdumay 4y ago
  It is important to point out that on his speech (and the book) he tells people to work on important problems (always on the plural), and that he never say not to work on non-important ones. In fact, I remember the book having a very clear assumption that you can't work on important things all the time anyway. But well, there has been some time since I've read it. But it is a very sensible and nuanced advice for highly ambitious people.
- emrah 4y ago
  > It does make sense to not work on incremental things for merely publications so it is definitely good advice. True but unfortunately this is how funding works based on what I saw during my time working at various labs. You need to provide enough evidence that what you are after is going to "work". Most of the brand new ideas get resources by repurposing data from existing funded projects. If you don't have what you need, you finangle the funded project to produce the data the new idea needs. I'm all for not syncing resources into crazy ideas that will never work but current state of affairs (it's getting worse) is too conservative
gumby 4y ago
I heard him give this talk at Ames back in the 80s. The advice and perspective are worth following even if you don’t plan to be a research scientist.
Calavar 4y ago
I think there is an enormous survivorship bias here. Research advances come in alternating of periods torrents and droughts, not in a steady trickle. Hamming, Shannon, and their contemporaries worked at a time of revolution in computer science. Let's put deep learning aside for a second. Can anyone here name a single academic in any other subfield of computer science who had a string of groundbreaking research works where every one of those works is from 1980 or after? I can't. And that's almost half a century that we're working with. Many people who defended their PhDs in the 1980s are already retired. This applies to plenty of other fields as well. Medicine, for instance: There were surgeons in the 1960s and 1970s who have half a dozen new surgical techniques to their name. (If you want some examples, look up Michael DeBakey, Mark Coventry, and Thomas Starzl.) You will not find a single academic surgeon today who comes even close to that, and at least in my opinion it's not because modern surgeons lack drive or creativity or the ambition to tackle big problems. Hamming is probably right that the role of luck in the sense of serendipity is overblown, but he ignores role of luck in the sense of structural factors that are out of your control. Because he and his colleagues largely operated in a context where all those structural factors were completely optimized. If you decide to start a PhD in a field 10 years before that field is destined to hit a multi-decade rut, if your advisor fails to make tenure partway through your PhD and your lab is shut down, if you get your first academic appointment in an environment where research funding is trending down and regulatory burdens are trending up, these are all factors that are by and large out of your control that can significantly alter the trajectory of your career.
- linguae 4y ago
  Indeed. The fact of the matter is that today’s environment for researchers is completely different from what it was like in 1986 when this talk was given, though I mention it not to take anything away from this talk. The days of places like Xerox PARC and Bell Labs where researchers had considerable freedom and autonomy are over and have been for quite some time now. Many industry labs promote business-driven research instead of purely curiosity-driven work and expect their researchers to produce a regular flow of research results that can be productized, lest they be shown the door. Academia these days isn’t exactly a bastion of freedom, either, with its “publish-or-perish” pressures needed to secure tenure and remain in good standing, as well as the need to raise grant money, both of which require pleasing external reviewers. Thus, successful researchers under this environment must find a way to manage the inevitable uncertainties of research while also producing enough output to make their evaluators happy. I find these “productivity” metrics stifling, but if I want to continue as a researcher, it’s either play the game successfully or find another way to make a living. I’ve been thinking long and hard about this for years. Perhaps researchers who value freedom of inquiry and freedom from “publish-or-perish” pressures could work independently, perhaps being funded by fellowships (like the MacArthur Grant), from part-time work, or from a side business.
dang 4y ago
A perennial. Here are the threads with comments (if anyone finds others, please let me know!): You and Your Research (1986) - https://news.ycombinator.com/item?id=31796353 https://news.ycombinator.com/item?id=31796353 - June 2022 (33 comments) You and Your Research – Richard Hamming - https://news.ycombinator.com/item?id=27451360 https://news.ycombinator.com/item?id=27451360 - June 2021 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=25242617 https://news.ycombinator.com/item?id=25242617 - Nov 2020 (1 comment) Richard Hamming: You and Your Research (1986) - https://news.ycombinator.com/item?id=24171820 https://news.ycombinator.com/item?id=24171820 - Aug 2020 (1 comment) You and Your Research – A talk by Richard W. Hamming [pdf] - https://news.ycombinator.com/item?id=23558974 https://news.ycombinator.com/item?id=23558974 - June 2020 (1 comment) You and Your Research by Richard Hamming (1995) [video] - https://news.ycombinator.com/item?id=18505884 https://news.ycombinator.com/item?id=18505884 - Nov 2018 (10 comments) You and Your Research (1986) - https://news.ycombinator.com/item?id=18014209 https://news.ycombinator.com/item?id=18014209 - Sept 2018 (10 comments) You and your research - https://news.ycombinator.com/item?id=14179317 https://news.ycombinator.com/item?id=14179317 - April 2017 (1 comment) You and Your Research, by Richard Hamming - https://news.ycombinator.com/item?id=10280198 https://news.ycombinator.com/item?id=10280198 - Sept 2015 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=9279585 https://news.ycombinator.com/item?id=9279585 - March 2015 (1 comment) Hamming, "You and Your Research" (1995) [video] - https://news.ycombinator.com/item?id=7683711 https://news.ycombinator.com/item?id=7683711 - May 2014 (25 comments) Video of Hamming's "You and Your Research" (1995) - https://news.ycombinator.com/item?id=5567448 https://news.ycombinator.com/item?id=5567448 - April 2013 (1 comment) Richard Hamming: You and Your Research (1986) - https://news.ycombinator.com/item?id=4626349 https://news.ycombinator.com/item?id=4626349 - Oct 2012 (27 comments) Richard Hamming: You and Your Research - https://news.ycombinator.com/item?id=3142978 https://news.ycombinator.com/item?id=3142978 - Oct 2011 (7 comments) You and Your Research - https://news.ycombinator.com/item?id=915515 https://news.ycombinator.com/item?id=915515 - Nov 2009 (5 comments) Richard Hamming - You and your research - https://news.ycombinator.com/item?id=852405 https://news.ycombinator.com/item?id=852405 - Sept 2009 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=625857 https://news.ycombinator.com/item?id=625857 - May 2009 (13 comments) You and Your Research (1986) - https://news.ycombinator.com/item?id=542023 https://news.ycombinator.com/item?id=542023 - April 2009 (4 comments) You and Your Research - https://news.ycombinator.com/item?id=524856 https://news.ycombinator.com/item?id=524856 - March 2009 (1 comment) Richard Hamming: You and Your Research - https://news.ycombinator.com/item?id=229067 https://news.ycombinator.com/item?id=229067 - June 2008 (7 comments) Why do so few scientists make significant contributions and so many are forgotten in the long run? - "You and Your Research" - https://news.ycombinator.com/item?id=52337 https://news.ycombinator.com/item?id=52337 - Sept 2007 (11 comments) You and Your (Great) Research - https://news.ycombinator.com/item?id=13218 https://news.ycombinator.com/item?id=13218 - April 2007 (6 comments) --- Note for anyone wondering: reposts are ok after a year or so (https://news.ycombinator.com/newsfaq.html https://news.ycombinator.com/newsfaq.html). I'll play the "or so" card and call this one ok. In addition to it being good for curiosity to revisit perennials sometimes (just not too often), HN is also a place for junior cohorts to have the pleasure of encountering the classics for the first time—an important function of the site!
scsteps 4y ago
I’ve always had trouble balancing between working on things that I consider to be important vs things that I am excited about. In my experience I’ve always gotten good results from the things I’m excited about and not what I consider to be important. Should I consider what I feel excited to be important? Personally, sure, but objectively speaking the world might not think that way.
- umutisik 4y ago
  What makes you excited about something in the case when it's not important?
mathisfun123 4y ago
There's a part of this that's never ever commented on >I don't like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There's no question about this. As someone that got married during their PhD and is now finishing up and reflecting: it isn't worth it. Neglecting the people in your life that love you in the pursuit of "science" is no different than neglecting them because you have a drug habit or because you're an inveterate gambler or because you're chasing fame and fortune. The science will get done regardless and the only thing you accomplish is ensuring your own interests. Suffice it to say I'm taking steps make sure my next gig has more room.
- JHonaker 4y ago
  It really isn't talked about enough. I am contemplating leaving my PhD despite being ABD with the majority of the interesting work done simply because the neglect it inflicts on my family is the cause of the overwhelming majority of conflicts in my life. I truly love working on the problem, investing time in research papers, and experimenting, but I have no desire to stay in academia. Plus, I have a well-paying full-time job (that I took during the pandemic to save my wife from having to shoulder our living expenses basically single-handedly while growing our child inside of her). > Suffice it to say I'm taking steps make sure my next gig has more room. I hear you. It's crazy how mentally abusive a lot of people's relationship with their PhD is. I'm convinced it's one of the reasons so many people with PhDs marry other PhDs. They're the only ones that "understand" the level of single-minded devotion you have to have to be an early career researcher.
- ke88y 4y ago
  As a PhD, I now believe that pursuing a career in science is an enormously selfish and entitled life choice for anyone who doesn't have a trust fund. It's not just neglect during the PhD. Even a non-neglectful academic is asking a lot of their partner. Stipends are low. Post-docs require chasing term-limited positions around the country, often with little to no savings, for up the half a decade. Building wealth is impossible, having a family is just barely possible, and the process takes you well into mid-life depriving your partner of a career and a real relationship. I have seen more divorces during post-docs than during PhDs. Everyone I know who made it through PhDs and post-docs without scars fell into one of two categories: unmarried or wealthy. I think academia's biggest open secret is that a HUGE number of academics -- especially in and around large metros or in nice climates -- are chasing a prestigious and comfortable job because their trust funds allow them to not care about the money and their upbringing makes it difficult for them to deal with having a manager.
pighive 4y ago
Thanks for sharing this, I came across the same material in a different format (either slides or may be a video couple of years back, can't exactly remember). What stuck to me is "If you are not working on an important problem, your work is not important". I tried to take a positive spin from this statement by considering whatever work I am currently doing is important enough to solve an important problem but it's really hard to convince yourself after some time when it is clearly not. Needless to say, I am still looking for that important problem.
lambdaloop 4y ago
It's funny, I was just thinking about this article this morning. When I first read it over 10 years ago, this quote really struck with me: > Another personality defect is ego assertion and I'll speak in this case of my own experience. I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, ``Why? No Vice President at IBM said, `Give Hamming a bad time'. It is the secretaries at the bottom who are doing this. When a slot appears, they'll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven't mistreated them.'' Answer, I wasn't dressing the way they felt somebody in that situation should. It came down to just that - I wasn't dressing properly. I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people. > Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Now you are going to tell me that somebody has to change the system. I agree; somebody's has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist. I tried to live that way for a couple years. Frankly, I think this way of living is unnecessarily restrictive. So what if you get slightly worse service? The clothes you wear and your expressions highlight your history and your culture. By self-censoring yourself, you end up just perpetuating the censorship of other views in the workplace. This goes double for scientists, as we are rather public facing and have room for wearing nontraditional clothes within our jobs.
- deleted 4y ago
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ssn 4y ago
Any recommendations on similar materials? I.e. advice on how to manage research.
- rg111 4y ago
  "How to Take Smart Notes" by Sanke Ahrens. Even if you decide not to use the Zettelkasten method, this book is still a great read.
- Sevan777 4y ago
  Currently reading The Sciences of the Artificial? by Herbert A. Simon
- qumpis 4y ago
  Also, any audiobooks about similar topics that are comfortable to listen to?
6451937099 4y ago
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anthomtb 4y ago
> I have now come down to a topic which is very distasteful; it is not sufficient to do a job, you have to sell it. `Selling' to a scientist is an awkward thing to do. It's very ugly; you shouldn't have to do it. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you've done, read it, and come back and say, ``Yes, that was good.'' I suggest that when you open a journal, as you turn the pages, you ask why you read some articles and not others. You had better write your report so when it is published in the Physical Review, or wherever else you want it, as the readers are turning the pages they won't just turn your pages but they will stop and read yours. If they don't stop and read it, you won't get credit. > There are three things you have to do in selling. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. We had a lot of so-called `back room scientists.' In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. They would not stand up right in the middle of a hot conference, in the middle of activity, and say, ``We should do this for these reasons.'' You need to master that form of communication as well as prepared speeches. I ran across this speech about 5 years into my software development career. These two paragraphs were a MAJOR game changer. Until then I could not believe that more than a minimum of soft skills were necessary being a developer and that my code would speak for itself. After reading Hamming's words I started putting much more effort into things like presentations and status emails. The results were not immediate and I am not exactly "next VP" but I am definitely in a stable and comfortable position in my current company. More importantly I am not frustrated when I write some cool-new-tool and nobody takes an interest. It almost certainly means there's nothing wrong with cool-new-tool and I need to better communicate what it is and why its useful. (Related: Hammings point about working on an important problem...your cool-new-tool may not actually be solving anything important).
istillwritecode 4y ago
Richard Hamming used to travel around and give that talk at every university he visited. I was lucky enough to hear him speak during my PhD studies around 1980.
photochemsyn 4y ago
It's not surprising this is from the early 1980s, right around the time Bayh-Dole was passed and before rampant corporatization of science really took hold, before the generation of profitable patents became the most important concern of leading public research institutions like MIT and the University of California. That, I suppose, is why the concept of 'academic fraud' doesn't appear once in the the talk, which is otherwise full of good general advice. However, fraudulent science is now a major problem in academia, and one of the worst took place some 15 years after this publication, at Bell Labs itself: https://en.wikipedia.org/wiki/Sch%C3%B6n_scandal https://en.wikipedia.org/wiki/Sch%C3%B6n_scandal If you're working in a lab and find the PI is fabricating data on a regular basis in order to get publications into journals, or so that they can be the first to claim a patent for a particular process, well, what's to be done? Hamming's comment doesn't really work in that case: > "Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time... Another thing you should look for is the positive side of things instead of the negative." Perhaps there was a Golden Age of Science in the past, when academic fraud wasn't fairly common and scientists weren't also entrepreneurs looking to market their dubious patents to large corporations for a percentage of the profits?
OldGuyInTheClub 4y ago
This (deservedly) famous article by a legend is a must-read but it is also like having Michael Jordan or Michael Phelps teaching how to be successful in basketball or swimming. What worked for them won't work for almost anyone else! FWIW, I was fortunate to do a postdoc at Bell Labs in the early 90s. The established and successful researchers, mostly men, would all talk about the sacrifices their wives made so that they could focus on meeting the insanely high expectations of the place in its glory days. It was the custom back when they made their reputations. The younger permanent staff members were leery of this because social mores and the nature of the research environment were both changing. The freewheeling pre-divestiture days were gone by that time and there was a pressure to be relevant to the needs of the corporation. The management still wanted publications in prestige journals and an international reputation by 35 but couldn't say how to do all that while satisfying the relevancy mandate. The stress on the younger permanent staff was palpable but they and everybody else made life delightful for us short-term appointees - it was all the things Universities ought to be. At the end of each Science Magazine issue is a "Working Life" feature where a (typically) young person writes about problems s/he is facing in launching a career. Work/family life balance is a consistent theme and more importantly an /expectation/ even for those on the tenure-track at high powered places. The times they have a-changed.
- _gmax0 4y ago
  Do you have any idea of where a young person might find that sort of environment today? Did you by chance work with Odlyzko there?
  - OldGuyInTheClub 4y ago
    I've been immersed in a very applied corner of industry for nearly 20 years now and have lost touch with the world of basic research. My sense (and I have no proof to offer) is that the old Bell/IBM/DuPont/GE/... era of industrial labs with a healthy exploration culture is gone and won't come back in my lifetime. - Seemed that Google had that spirit at one time with its X Lab and also the Google Labs that put out fun products but all I read here and elsewhere is that is in the past - The Janelia Research Campus may be carrying on the spirit of small, collaborative groups led by a hands-on scientist (there were no empires at Bell Labs.) Could be a very good place to be a young student that has an interest in biology, instrumentation, and/or computation. See what they expect from the lab heads here: https://www.janelia.org/our-research/our-labs/group-leaders https://www.janelia.org/our-research/our-labs/group-leaders /excerpt "Group Leaders have time to focus their energy and creativity on research with the freedom to pursue long-term difficult projects through collaborative, interdisciplinary work. They are not evaluated solely on conventional academic measures, such as publishing. Rather, Group Leaders will be expected to make progress in their research areas and make contributions to the work of other Janelia scientists through collaboration, constructive criticism, or mentoring." /excerpt One of the guys I did know personally wound up at Janelia and eventually at Stockholm. I was on the other side of the very long Murray Hill building in the physical sciences area. I went to one of Odlyzko's presentations at the Journal Club circa 1992 or 1993 - I think it was on an important new result in prime numbers/factorization/encryption. I never met him, let alone worked with him, though. I do remember one of my senior colleagues (physical scientist) wondering why any of that stuff mattered. My response was that it was probably much more important than anything he or I were doing, had done, or would ever do. I had read something in Byte or a similar popular magazine about primes and encryption it seemed like the field had serious practical implications on top of being incredibly interesting. One of the few correct predictions in my career! Addendum: On re-reading this, I realized that I am taking a very US-centric perspective. The spirit/culture I was talking about could exist in other countries.
whatrocks 4y ago
A favorite of mine! My friend Oz (of teachyourselfcs.com) and I chatted about this talk in the first episode of our show - focusing on how Oz has seen its influence and impact on the early/mid-career software engineers he's taught: https://show.csprimer.com/episodes/e1-doing-meaningful-work https://show.csprimer.com/episodes/e1-doing-meaningful-work
deleted 4y ago
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186 points by ftxbro 4y ago

Here's a recording from '95 entitled the same: https://www.youtube.com/watch?v=a1zDuOPkMSw https://www.youtube.com/watch?v=a1zDuOPkMSw I also highly recommend reading the Stripe Press book also with the same name: https://www.amazon.com/dp/1732265178 https://www.amazon.com/dp/1732265178

netcraft 4y ago
I came to also recommend the book. The last half is about specific engineering topics, but the first half is packed with great ideas and thoughts that anyone will find valuable. Its also a beautiful and well made book.
teddyh 4y ago
Better video quality, same source material: https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR89bl7hTOS3F3wuoGj7id3Xy&index=32#t=22s https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR...

shae 4y ago

Get the book! It's packed with great content.

teddyh 4y ago

On video: https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR89bl7hTOS3F3wuoGj7id3Xy&index=32#t=22s https://www.youtube.com/watch?v=e3msMuwqp-o&list=PLctkxgWNSR...

reachtarunhere 4y ago

One of the points of the talk is emphasis on working on "important" problems. It does make sense to not work on incremental things for merely publications so it is definitely good advice. However once you decide to do so what is "important" becomes a difficult question. I like this article from Daniel Lemire which explores this further https://lemire.me/blog/2010/03/22/so-you-know-whats-important/ https://lemire.me/blog/2010/03/22/so-you-know-whats-importan...

Swizec 4y ago
The way I’ve always interpreted this is that if even you don’t think it’s important, why are you doing it? Sure you can’t accurately predict what will and won’t be important long term, but you should think your work is important. Whether you’re right or wrong time will tell.
- reachtarunhere 4y ago
  Yes my interpretation is that this is more an advice on what not to do - frivolous stuff you don't believe in
marcosdumay 4y ago
It is important to point out that on his speech (and the book) he tells people to work on important problems (always on the plural), and that he never say not to work on non-important ones. In fact, I remember the book having a very clear assumption that you can't work on important things all the time anyway. But well, there has been some time since I've read it. But it is a very sensible and nuanced advice for highly ambitious people.
emrah 4y ago
> It does make sense to not work on incremental things for merely publications so it is definitely good advice. True but unfortunately this is how funding works based on what I saw during my time working at various labs. You need to provide enough evidence that what you are after is going to "work". Most of the brand new ideas get resources by repurposing data from existing funded projects. If you don't have what you need, you finangle the funded project to produce the data the new idea needs. I'm all for not syncing resources into crazy ideas that will never work but current state of affairs (it's getting worse) is too conservative

gumby 4y ago

I heard him give this talk at Ames back in the 80s. The advice and perspective are worth following even if you don’t plan to be a research scientist.

Calavar 4y ago

I think there is an enormous survivorship bias here. Research advances come in alternating of periods torrents and droughts, not in a steady trickle. Hamming, Shannon, and their contemporaries worked at a time of revolution in computer science. Let's put deep learning aside for a second. Can anyone here name a single academic in any other subfield of computer science who had a string of groundbreaking research works where every one of those works is from 1980 or after? I can't. And that's almost half a century that we're working with. Many people who defended their PhDs in the 1980s are already retired. This applies to plenty of other fields as well. Medicine, for instance: There were surgeons in the 1960s and 1970s who have half a dozen new surgical techniques to their name. (If you want some examples, look up Michael DeBakey, Mark Coventry, and Thomas Starzl.) You will not find a single academic surgeon today who comes even close to that, and at least in my opinion it's not because modern surgeons lack drive or creativity or the ambition to tackle big problems. Hamming is probably right that the role of luck in the sense of serendipity is overblown, but he ignores role of luck in the sense of structural factors that are out of your control. Because he and his colleagues largely operated in a context where all those structural factors were completely optimized. If you decide to start a PhD in a field 10 years before that field is destined to hit a multi-decade rut, if your advisor fails to make tenure partway through your PhD and your lab is shut down, if you get your first academic appointment in an environment where research funding is trending down and regulatory burdens are trending up, these are all factors that are by and large out of your control that can significantly alter the trajectory of your career.

linguae 4y ago
Indeed. The fact of the matter is that today’s environment for researchers is completely different from what it was like in 1986 when this talk was given, though I mention it not to take anything away from this talk. The days of places like Xerox PARC and Bell Labs where researchers had considerable freedom and autonomy are over and have been for quite some time now. Many industry labs promote business-driven research instead of purely curiosity-driven work and expect their researchers to produce a regular flow of research results that can be productized, lest they be shown the door. Academia these days isn’t exactly a bastion of freedom, either, with its “publish-or-perish” pressures needed to secure tenure and remain in good standing, as well as the need to raise grant money, both of which require pleasing external reviewers. Thus, successful researchers under this environment must find a way to manage the inevitable uncertainties of research while also producing enough output to make their evaluators happy. I find these “productivity” metrics stifling, but if I want to continue as a researcher, it’s either play the game successfully or find another way to make a living. I’ve been thinking long and hard about this for years. Perhaps researchers who value freedom of inquiry and freedom from “publish-or-perish” pressures could work independently, perhaps being funded by fellowships (like the MacArthur Grant), from part-time work, or from a side business.

dang 4y ago

A perennial. Here are the threads with comments (if anyone finds others, please let me know!): You and Your Research (1986) - https://news.ycombinator.com/item?id=31796353 https://news.ycombinator.com/item?id=31796353 - June 2022 (33 comments) You and Your Research – Richard Hamming - https://news.ycombinator.com/item?id=27451360 https://news.ycombinator.com/item?id=27451360 - June 2021 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=25242617 https://news.ycombinator.com/item?id=25242617 - Nov 2020 (1 comment) Richard Hamming: You and Your Research (1986) - https://news.ycombinator.com/item?id=24171820 https://news.ycombinator.com/item?id=24171820 - Aug 2020 (1 comment) You and Your Research – A talk by Richard W. Hamming [pdf] - https://news.ycombinator.com/item?id=23558974 https://news.ycombinator.com/item?id=23558974 - June 2020 (1 comment) You and Your Research by Richard Hamming (1995) [video] - https://news.ycombinator.com/item?id=18505884 https://news.ycombinator.com/item?id=18505884 - Nov 2018 (10 comments) You and Your Research (1986) - https://news.ycombinator.com/item?id=18014209 https://news.ycombinator.com/item?id=18014209 - Sept 2018 (10 comments) You and your research - https://news.ycombinator.com/item?id=14179317 https://news.ycombinator.com/item?id=14179317 - April 2017 (1 comment) You and Your Research, by Richard Hamming - https://news.ycombinator.com/item?id=10280198 https://news.ycombinator.com/item?id=10280198 - Sept 2015 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=9279585 https://news.ycombinator.com/item?id=9279585 - March 2015 (1 comment) Hamming, "You and Your Research" (1995) [video] - https://news.ycombinator.com/item?id=7683711 https://news.ycombinator.com/item?id=7683711 - May 2014 (25 comments) Video of Hamming's "You and Your Research" (1995) - https://news.ycombinator.com/item?id=5567448 https://news.ycombinator.com/item?id=5567448 - April 2013 (1 comment) Richard Hamming: You and Your Research (1986) - https://news.ycombinator.com/item?id=4626349 https://news.ycombinator.com/item?id=4626349 - Oct 2012 (27 comments) Richard Hamming: You and Your Research - https://news.ycombinator.com/item?id=3142978 https://news.ycombinator.com/item?id=3142978 - Oct 2011 (7 comments) You and Your Research - https://news.ycombinator.com/item?id=915515 https://news.ycombinator.com/item?id=915515 - Nov 2009 (5 comments) Richard Hamming - You and your research - https://news.ycombinator.com/item?id=852405 https://news.ycombinator.com/item?id=852405 - Sept 2009 (1 comment) You and Your Research - https://news.ycombinator.com/item?id=625857 https://news.ycombinator.com/item?id=625857 - May 2009 (13 comments) You and Your Research (1986) - https://news.ycombinator.com/item?id=542023 https://news.ycombinator.com/item?id=542023 - April 2009 (4 comments) You and Your Research - https://news.ycombinator.com/item?id=524856 https://news.ycombinator.com/item?id=524856 - March 2009 (1 comment) Richard Hamming: You and Your Research - https://news.ycombinator.com/item?id=229067 https://news.ycombinator.com/item?id=229067 - June 2008 (7 comments) Why do so few scientists make significant contributions and so many are forgotten in the long run? - "You and Your Research" - https://news.ycombinator.com/item?id=52337 https://news.ycombinator.com/item?id=52337 - Sept 2007 (11 comments) You and Your (Great) Research - https://news.ycombinator.com/item?id=13218 https://news.ycombinator.com/item?id=13218 - April 2007 (6 comments) --- Note for anyone wondering: reposts are ok after a year or so (https://news.ycombinator.com/newsfaq.html https://news.ycombinator.com/newsfaq.html). I'll play the "or so" card and call this one ok. In addition to it being good for curiosity to revisit perennials sometimes (just not too often), HN is also a place for junior cohorts to have the pleasure of encountering the classics for the first time—an important function of the site!

scsteps 4y ago

I’ve always had trouble balancing between working on things that I consider to be important vs things that I am excited about. In my experience I’ve always gotten good results from the things I’m excited about and not what I consider to be important. Should I consider what I feel excited to be important? Personally, sure, but objectively speaking the world might not think that way.

umutisik 4y ago
What makes you excited about something in the case when it's not important?

mathisfun123 4y ago

There's a part of this that's never ever commented on >I don't like to say it in front of my wife, but I did sort of neglect her sometimes; I needed to study. You have to neglect things if you intend to get what you want done. There's no question about this. As someone that got married during their PhD and is now finishing up and reflecting: it isn't worth it. Neglecting the people in your life that love you in the pursuit of "science" is no different than neglecting them because you have a drug habit or because you're an inveterate gambler or because you're chasing fame and fortune. The science will get done regardless and the only thing you accomplish is ensuring your own interests. Suffice it to say I'm taking steps make sure my next gig has more room.

JHonaker 4y ago
It really isn't talked about enough. I am contemplating leaving my PhD despite being ABD with the majority of the interesting work done simply because the neglect it inflicts on my family is the cause of the overwhelming majority of conflicts in my life. I truly love working on the problem, investing time in research papers, and experimenting, but I have no desire to stay in academia. Plus, I have a well-paying full-time job (that I took during the pandemic to save my wife from having to shoulder our living expenses basically single-handedly while growing our child inside of her). > Suffice it to say I'm taking steps make sure my next gig has more room. I hear you. It's crazy how mentally abusive a lot of people's relationship with their PhD is. I'm convinced it's one of the reasons so many people with PhDs marry other PhDs. They're the only ones that "understand" the level of single-minded devotion you have to have to be an early career researcher.
ke88y 4y ago
As a PhD, I now believe that pursuing a career in science is an enormously selfish and entitled life choice for anyone who doesn't have a trust fund. It's not just neglect during the PhD. Even a non-neglectful academic is asking a lot of their partner. Stipends are low. Post-docs require chasing term-limited positions around the country, often with little to no savings, for up the half a decade. Building wealth is impossible, having a family is just barely possible, and the process takes you well into mid-life depriving your partner of a career and a real relationship. I have seen more divorces during post-docs than during PhDs. Everyone I know who made it through PhDs and post-docs without scars fell into one of two categories: unmarried or wealthy. I think academia's biggest open secret is that a HUGE number of academics -- especially in and around large metros or in nice climates -- are chasing a prestigious and comfortable job because their trust funds allow them to not care about the money and their upbringing makes it difficult for them to deal with having a manager.

pighive 4y ago

Thanks for sharing this, I came across the same material in a different format (either slides or may be a video couple of years back, can't exactly remember). What stuck to me is "If you are not working on an important problem, your work is not important". I tried to take a positive spin from this statement by considering whatever work I am currently doing is important enough to solve an important problem but it's really hard to convince yourself after some time when it is clearly not. Needless to say, I am still looking for that important problem.

lambdaloop 4y ago

It's funny, I was just thinking about this article this morning. When I first read it over 10 years ago, this quote really struck with me: > Another personality defect is ego assertion and I'll speak in this case of my own experience. I came from Los Alamos and in the early days I was using a machine in New York at 590 Madison Avenue where we merely rented time. I was still dressing in western clothes, big slash pockets, a bolo and all those things. I vaguely noticed that I was not getting as good service as other people. So I set out to measure. You came in and you waited for your turn; I felt I was not getting a fair deal. I said to myself, ``Why? No Vice President at IBM said, `Give Hamming a bad time'. It is the secretaries at the bottom who are doing this. When a slot appears, they'll rush to find someone to slip in, but they go out and find somebody else. Now, why? I haven't mistreated them.'' Answer, I wasn't dressing the way they felt somebody in that situation should. It came down to just that - I wasn't dressing properly. I had to make the decision - was I going to assert my ego and dress the way I wanted to and have it steadily drain my effort from my professional life, or was I going to appear to conform better? I decided I would make an effort to appear to conform properly. The moment I did, I got much better service. And now, as an old colorful character, I get better service than other people. > Many a second-rate fellow gets caught up in some little twitting of the system, and carries it through to warfare. He expends his energy in a foolish project. Now you are going to tell me that somebody has to change the system. I agree; somebody's has to. Which do you want to be? The person who changes the system or the person who does first-class science? Which person is it that you want to be? Be clear, when you fight the system and struggle with it, what you are doing, how far to go out of amusement, and how much to waste your effort fighting the system. My advice is to let somebody else do it and you get on with becoming a first-class scientist. Very few of you have the ability to both reform the system and become a first-class scientist. I tried to live that way for a couple years. Frankly, I think this way of living is unnecessarily restrictive. So what if you get slightly worse service? The clothes you wear and your expressions highlight your history and your culture. By self-censoring yourself, you end up just perpetuating the censorship of other views in the workplace. This goes double for scientists, as we are rather public facing and have room for wearing nontraditional clothes within our jobs.

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ssn 4y ago

Any recommendations on similar materials? I.e. advice on how to manage research.

rg111 4y ago
"How to Take Smart Notes" by Sanke Ahrens. Even if you decide not to use the Zettelkasten method, this book is still a great read.
Sevan777 4y ago
Currently reading The Sciences of the Artificial? by Herbert A. Simon
qumpis 4y ago
Also, any audiobooks about similar topics that are comfortable to listen to?

6451937099 4y ago

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anthomtb 4y ago

> I have now come down to a topic which is very distasteful; it is not sufficient to do a job, you have to sell it. `Selling' to a scientist is an awkward thing to do. It's very ugly; you shouldn't have to do it. The world is supposed to be waiting, and when you do something great, they should rush out and welcome it. But the fact is everyone is busy with their own work. You must present it so well that they will set aside what they are doing, look at what you've done, read it, and come back and say, ``Yes, that was good.'' I suggest that when you open a journal, as you turn the pages, you ask why you read some articles and not others. You had better write your report so when it is published in the Physical Review, or wherever else you want it, as the readers are turning the pages they won't just turn your pages but they will stop and read yours. If they don't stop and read it, you won't get credit. > There are three things you have to do in selling. You have to learn to write clearly and well so that people will read it, you must learn to give reasonably formal talks, and you also must learn to give informal talks. We had a lot of so-called `back room scientists.' In a conference, they would keep quiet. Three weeks later after a decision was made they filed a report saying why you should do so and so. Well, it was too late. They would not stand up right in the middle of a hot conference, in the middle of activity, and say, ``We should do this for these reasons.'' You need to master that form of communication as well as prepared speeches. I ran across this speech about 5 years into my software development career. These two paragraphs were a MAJOR game changer. Until then I could not believe that more than a minimum of soft skills were necessary being a developer and that my code would speak for itself. After reading Hamming's words I started putting much more effort into things like presentations and status emails. The results were not immediate and I am not exactly "next VP" but I am definitely in a stable and comfortable position in my current company. More importantly I am not frustrated when I write some cool-new-tool and nobody takes an interest. It almost certainly means there's nothing wrong with cool-new-tool and I need to better communicate what it is and why its useful. (Related: Hammings point about working on an important problem...your cool-new-tool may not actually be solving anything important).

istillwritecode 4y ago

Richard Hamming used to travel around and give that talk at every university he visited. I was lucky enough to hear him speak during my PhD studies around 1980.

photochemsyn 4y ago

It's not surprising this is from the early 1980s, right around the time Bayh-Dole was passed and before rampant corporatization of science really took hold, before the generation of profitable patents became the most important concern of leading public research institutions like MIT and the University of California. That, I suppose, is why the concept of 'academic fraud' doesn't appear once in the the talk, which is otherwise full of good general advice. However, fraudulent science is now a major problem in academia, and one of the worst took place some 15 years after this publication, at Bell Labs itself: https://en.wikipedia.org/wiki/Sch%C3%B6n_scandal https://en.wikipedia.org/wiki/Sch%C3%B6n_scandal If you're working in a lab and find the PI is fabricating data on a regular basis in order to get publications into journals, or so that they can be the first to claim a patent for a particular process, well, what's to be done? Hamming's comment doesn't really work in that case: > "Another fault is anger. Often a scientist becomes angry, and this is no way to handle things. Amusement, yes, anger, no. Anger is misdirected. You should follow and cooperate rather than struggle against the system all the time... Another thing you should look for is the positive side of things instead of the negative." Perhaps there was a Golden Age of Science in the past, when academic fraud wasn't fairly common and scientists weren't also entrepreneurs looking to market their dubious patents to large corporations for a percentage of the profits?

OldGuyInTheClub 4y ago

This (deservedly) famous article by a legend is a must-read but it is also like having Michael Jordan or Michael Phelps teaching how to be successful in basketball or swimming. What worked for them won't work for almost anyone else! FWIW, I was fortunate to do a postdoc at Bell Labs in the early 90s. The established and successful researchers, mostly men, would all talk about the sacrifices their wives made so that they could focus on meeting the insanely high expectations of the place in its glory days. It was the custom back when they made their reputations. The younger permanent staff members were leery of this because social mores and the nature of the research environment were both changing. The freewheeling pre-divestiture days were gone by that time and there was a pressure to be relevant to the needs of the corporation. The management still wanted publications in prestige journals and an international reputation by 35 but couldn't say how to do all that while satisfying the relevancy mandate. The stress on the younger permanent staff was palpable but they and everybody else made life delightful for us short-term appointees - it was all the things Universities ought to be. At the end of each Science Magazine issue is a "Working Life" feature where a (typically) young person writes about problems s/he is facing in launching a career. Work/family life balance is a consistent theme and more importantly an /expectation/ even for those on the tenure-track at high powered places. The times they have a-changed.

_gmax0 4y ago
Do you have any idea of where a young person might find that sort of environment today? Did you by chance work with Odlyzko there?
- OldGuyInTheClub 4y ago
  I've been immersed in a very applied corner of industry for nearly 20 years now and have lost touch with the world of basic research. My sense (and I have no proof to offer) is that the old Bell/IBM/DuPont/GE/... era of industrial labs with a healthy exploration culture is gone and won't come back in my lifetime. - Seemed that Google had that spirit at one time with its X Lab and also the Google Labs that put out fun products but all I read here and elsewhere is that is in the past - The Janelia Research Campus may be carrying on the spirit of small, collaborative groups led by a hands-on scientist (there were no empires at Bell Labs.) Could be a very good place to be a young student that has an interest in biology, instrumentation, and/or computation. See what they expect from the lab heads here: https://www.janelia.org/our-research/our-labs/group-leaders https://www.janelia.org/our-research/our-labs/group-leaders /excerpt "Group Leaders have time to focus their energy and creativity on research with the freedom to pursue long-term difficult projects through collaborative, interdisciplinary work. They are not evaluated solely on conventional academic measures, such as publishing. Rather, Group Leaders will be expected to make progress in their research areas and make contributions to the work of other Janelia scientists through collaboration, constructive criticism, or mentoring." /excerpt One of the guys I did know personally wound up at Janelia and eventually at Stockholm. I was on the other side of the very long Murray Hill building in the physical sciences area. I went to one of Odlyzko's presentations at the Journal Club circa 1992 or 1993 - I think it was on an important new result in prime numbers/factorization/encryption. I never met him, let alone worked with him, though. I do remember one of my senior colleagues (physical scientist) wondering why any of that stuff mattered. My response was that it was probably much more important than anything he or I were doing, had done, or would ever do. I had read something in Byte or a similar popular magazine about primes and encryption it seemed like the field had serious practical implications on top of being incredibly interesting. One of the few correct predictions in my career! Addendum: On re-reading this, I realized that I am taking a very US-centric perspective. The spirit/culture I was talking about could exist in other countries.

whatrocks 4y ago

A favorite of mine! My friend Oz (of teachyourselfcs.com) and I chatted about this talk in the first episode of our show - focusing on how Oz has seen its influence and impact on the early/mid-career software engineers he's taught: https://show.csprimer.com/episodes/e1-doing-meaningful-work https://show.csprimer.com/episodes/e1-doing-meaningful-work

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