7 ms·

On Impactful AI Research

255 points by KraftyOne 2y ago

will-burner 2y ago
This has good advice about academic research in general not just AI Research. It's huge to "Select timely problems with large headroom and "fanout"" - you need a research program to have a successful research career. At least most people do. It's also huge to "Put your work out there and own popularizing your ideas" - the second part is hard for a lot of academics to do. Putting your work out there is huge to get feedback, which may help you pivot or try different directions, as well as fostering collaboration. Collaboration is a large part of being a successful researcher.
- Loic 2y ago
  > Collaboration is a large part of being a successful researcher. I would even consider it as the largest part. It brings ideas, funding, spreading of your ideas, access to institutional research grants/projects, industry contacts, and more.
  - Blahah 2y ago
    Agreed! It also brings friendships, new ways of thinking and framing, inspiration, and the opportunity to give and receive support - to discover how much you can matter, and the good you can do.
    - dkga 2y ago
      Completely second that and the parent comment! Not to mention it’s a good way to have an excuse for a glass of champagne or wine when you finally meet remote co-authors.
  - space_oddity 2y ago
    The lifeblood of a successful research career.
- vaylian 2y ago
  > you need a research program What is a "research program"?
  - throw_pm23 2y ago
    the "concepts of a plan"
  - antognini 2y ago
    The idea is that rather than doing a bunch of completely independent research projects, all of your projects are designed in service of answering some larger research question.
- deleted 2y ago
  [deleted]
- space_oddity 2y ago
  I think many great ideas never gain traction simply because they weren’t communicated effectively
tony_cannistra 2y ago
"Invest in projects, not papers." This is excellent advice, and in my experience does not represent the intuition that many young (and not so young) researchers begin with. Papers come from projects and, if you care, good projects can yield many good papers!
- juujian 2y ago
  Idk, nothing wrong with going for a low-hanging fruit and doing a one-off sometimes. So many academics fail to get stuff over the finish line. Not the right advice for everybody.
  - danielmarkbruce 2y ago
    Interesting. This is a common problem in academia?
    - juujian 2y ago
      Depends on the person. Not unheard of to see people with 10+ working papers that realistically will never see the light of day. Each of those are months of work.
      - danielmarkbruce 2y ago
        I can see that I guess. Easier to start a new one than do the annoying parts to finish one.
  - stavros 2y ago
    Yeah, but it's not saying "don't do papers", it's saying your long-term investment should be projects.
  - tony_cannistra 2y ago
    nothing wrong except that it might be a distraction, which sometimes is good and sometimes would be better avoided.
vouaobrasil 2y ago
> how do I do research that makes a difference in the current, rather crowded AI space? I hope they are first asking, to which bank accounts is the research actually making a difference? It's a great fraud to present research problems to stimulate the intellect of the naive youth when they have no capability to assess its social impact.
- deleted 2y ago
  [deleted]
KuriousCat 2y ago
I would say follow the money, create a product or service that generates recurrent income and channel that income to study the fundamental problems that would interest you. Owning a product or platform opens up for a lot of opportunities.
- Ar-Curunir 2y ago
  Thankfully research is not guided by notions like "what makes money in the current economy"; otherwise we'd be stuck with faster calculators instead of, well, all of modern computer science.
  - Maxatar 2y ago
    Most research I know about in academia is absolutely about what makes money.
    - Ar-Curunir 2y ago
      Care to give some examples? It is largely untrue in CS academia, and definitely untrue in every other non-engineering field.
  - KuriousCat 2y ago
    I did not say anything about making money in the current economy. Research requires funding and only way to have academic freedom is to have a steady source of recurrent income or funding. One way to get that is to please those who have money but give up part of your control on what you study. Other way is to monetize your knowledge and acquire a ton of money. You seem to misunderstand what I said or have very little clue on how the academia works.
  - godelski 2y ago
    > Thankfully research is not guided by notions like "what makes money in the current economy" Unfortunately I don't believe this is true for AI research... I think you'll find a strong correlation with each year's most cited papers and what's currently popular in industry. There's always exceptions, but we moved to a world where we're highly benchmark oriented, and that means we're highly reliant on having large compute infrastructures, and that means that the access and/or funding comes from industry. Who is obviously going to pressure research directions towards certain things.
Der_Einzige 2y ago
At least some of it comes from "hype" too. The author of Dspy (the writer) (https://github.com/stanfordnlp/dspy https://github.com/stanfordnlp/dspy) should know this, given that Dspy is nothing more than fancy prompts optimizing prompts to be fancier according to prompt chains described in papers (i.e. Chain of thought, Tree of thought, etc). Textgrad (https://github.com/zou-group/textgrad https://github.com/zou-group/textgrad) is an even worse example of this, as it makes people think that it's not just a prompt optimizing another prompt Dspy has 17k stars, meanwhile PyReft (https://github.com/stanfordnlp/pyreft https://github.com/stanfordnlp/pyreft) isn't even at 1200 yet and it has Christopher Manning (head of AI at stanford) working on it (see their paper: https://arxiv.org/abs/2404.03592 https://arxiv.org/abs/2404.03592). Sometimes what the world deems "impactful" in the short-medium term is wrong. Think long term. PyReft is likely the beginning of an explosion in demand for ultra parameter efficient techniques, while Dspy will likely fade into obscurity over time. I also know that the folks writing better samplers/optimizers for LLMs get almost no love/credit relative to the outsized impact they have on the field. A new sampler potentially improves EVERY LLM EVER! Folks like Clara Meister or the authors of the min_p paper preprint have had far larger impacts on the field than their citation counts might suggest, based on the fact that typiciality or min_p sampling is now considered generally superior to top_p/top_k (OpenAI, Anthropic, Gemini, et al still use top_p/top_k) and min_p/typicality are implemented by every open source LLM inference engine (i.e. huggingface, vllm, sglang, etc)
- thelastbender12 2y ago
  I think that's a little harsh. Imo the reason for difference in popularity/github-stars is just different user bases- an order of magnitude more people use LLM APIs (and can leverage Dspy) vs those who finetune an LLM. Agree about the abstractions btw. I found Dspy very convoluted for what it does, couldn't make sense of Textgrad at all.
sashank_1509 2y ago
Unfortunately while this advice sounds useful, it isn’t. It might be useful if you measure impact is the fake metrics like citation count but if you want to measure with actual tangible impact on the real world, you have a rude awakening before you. To me there are 2 ways a paper can create impact: 1. The paper represents such an impressive leap in performance over existing methods in AI, that it is obviously impactful. Unfortunately, this way of generating impact is dominated by industry. No one can expect Academia to train O1, SAM, GPT5 etc. AI rewards scale, scale requires money, resources and manpower and Academia has none. In the early days of AI, there were rare moments when this was possible, AlexNet, Adam, Transformers, PPO etc. Is it still possible? I do not know, I have not seen anything in the last 3 years and I’m not optimistic many such opportunities are left. Even validating your idea tends to require the scale of industry. 2. The paper affects the thought process of other AI researchers and thus you are indirectly impactful if any of them cause big leaps in AI performance. Unfortunately here is where Academia has shot itself in the foot by generating so many damn papers every year (>10,000). There are just so many, that the effect of any 1 paper is meaningless. In fact the only way to be impactful now is to be in a social circle of great researchers, so that you know your social circle will read your paper and later if any of them make big performance improvements, you can believe that you played a small role in it. I have spoken to a lot of ML researchers, and they told me they choose papers to read just based on people and research groups they know. Even being a NeurIPS spotlight paper, means less than 10% of researchers will read your paper, maybe it will go to 50% if it’s a NEURIPS best paper but even that I doubt. How many researchers remember last year’s NEURIPS best paper? The only solution to problem 2, is radical. The ML community needs to come together and limit the number of papers it wide releases. Let us say it came out and said that yearly only 20 curated papers will be widely published. Then you can bet most of the ML community will read all 20 of those papers and engage with it deeply as they will be capable of spending more than a day at least thinking about the paper. Of course you can still publish on arxiv, share with friends etc but unless such a dramatic cutdown is made I don’t see how you can be an actually impactful AI researcher in Academia when option 1 is too expensive and option 2 is made impossible.
- EnigmaFlare 2y ago
  If you were a really good academic, you could come up with a theory that predicts the performance of a model you haven't actually tested. Physics is full of this - theories that predict something novel followed by other people doing expensive experiments to test them. The guy who published the theory gets the credit. That's probably what we want from academic AI researchers - theories that we can eventually use to design models, rather than just haphazardly building something and wondering how good it will be.
lmeyerov 2y ago
I like the article directionally but fear the examples are too short-sighted for most AI researchers. Picking something useful in 1-2 years is a reason to go to industry, not research, and leads to mostly incremental units that if you don't do, someone else will. Yes, hot topics are good because they signal a time of fertile innovation. But not if your vision is so shallow that you will have half of IBM, Google, and YC competing with you before you start or by the time of your first publication (6-12mo). If you are a top student, well-educated already, with top resources and your own mentees, and your advisor is an industry leader who already knows where your work will go, maybe go to the thickest 1-2 year out AI VC fest, but that's not most PhD students. A 'practical' area would be obvious to everyone in 5 years, but winnowing out the crowd, there should not be much point to it today nor 1-2 years without something fundamentally changing. It should be tangible enough to be relevant and enticing, but too expensive for whatever reasons. More fundamental research would be even more years out. This gives you a year or two to dig into the problem, and another year or two to build out fundamental solutions, and then a couple years of cranking. From there, rinse-and-repeat via your own career or those of your future students. Some of my favorite work took 1-2 years of research to establish the problem, not just the solutions. Two of the projects here were weird at first as problems on a longer time scale, but ended up as part of $20M grant and software many folks here use & love, and another, a 10 year test of time award. (And another, arguably a $100M+ division at Nvidia). In contrast, most of my topic-of-the-year stuff didn't matter and was interchangeable with work by others. Edit: The speech by Hamming on "You and your research" hits on similar themes and speaks more to my experiences here: https://fs.blog/great-talks/richard-hamming-your-research/ https://fs.blog/great-talks/richard-hamming-your-research/
- QuadmasterXLII 2y ago
  If no one did the research that anyone could do, it would never get done.
  - marcosdumay 2y ago
    In most markets, it pays to be contrarian. ... and when everybody decides to be a contrarian, the contrarian position is to do the popular thing. But the catch is that this never happens on practice.
spatalo 2y ago
i don't fully agree with the headroom, many papers were published achieving 1% improvement on ImageNet...
- Nevermark 2y ago
  Agreed. Any improvement in a well established and competitive metric which a community is tracking is going to get attention and respect.
low_tech_love 2y ago
Although point #1 is true, I find it to be a slightly superficial advice. It's like saying "if you want to be happy, find a job that fulfills you". Sure, everyone wants to be able to focus on good projects before papers, so that the papers come naturally. If you can do that, congrats! You won the game; be proud and enjoy it. However, the truth is that the way to get there is dark and lonely and full of terrors, and not everyone can do it. All academics (especially junior ones) are constantly in the middle of an ambiguous, contradictory discourse: you must produce a lot, but you also must produce high-quality output. Your environment, literally everyone around you, wants to have your cake and eat it too. As you get more experienced you learn to navigate this and keep the good parts while ignoring the bad ones, but for young researchers this can be extremely taxing and stressful. In order to "focus on projects and not papers" you have to literally swim against the current, usually in a very very strong current. Not everyone has the presence of mind and attitude to do it, and to be honest, it's not fair to expect that either. So, here are some points and comments I offer that go in a slightly different direction (although, like I said, if you managed to get there, congrats!): * You can write a good paper without it being a good project. One thing does not exclude the other, and the fact that there are many bad papers out there does not mean that papers themselves are bad. You can plan your work around a paper, do a good research job, and write a good scientific report without having to have an overarching research project that spills over that. Sure, it is great when it happens (and it will happen the more experienced and senior you get), but it's not necessarily true. * Not thinking about the paper you'll write out of your work might deter you from operationalizing your research correctly. Not every project can be translated into a good research paper, with objective/concrete measurements that translate to a good scientific report. You might end up with a good Github repo (with lots of stars and forks) and if that's your goal, then great! But if your goal is to publish, you need to think early on: "what can I do that will be translated into a good scientific paper later?" This will guide your methods towards the right direction and make sure you do not pull your hair later (at least not as many) when you get rejected a million times and end up putting your paper in a venue you're not proud of. * Publishing papers generates motivation. When a young research goes too long without seeing the results of their work, they lose motivation. It's very common for students to have this philosophical stance that they want to work on the next big project that will change the world, and that they need time and comfort and peace to do that, so please don't bother me with this "paper" talk. Fast forward three years later they have nothing published, are depressed, and spend their time playing video games and procrastinating. The fact is that people see other people moving forward, and if they don't, no amount of willpower to "save the world" with a big project will keep them going. Publishing papers gives motivation; you feel that your work was worth it, you go to conferences and talk to people, you hear feedback from the community. It's extremely important, and there's no world where a PhD student without papers is healthier and happier than one with papers. * Finishing a paper and starting the next one is a healthy work discipline. Some people just want to write a good paper and move on. Not everyone feels so passionate about their work that they want to spend their personal time with it, and push it over all boundaries. You don't have to turn your work into your entire life. Doing a good job and then moving on is a very healthy practice.
mehulashah 2y ago
This advice is much more general than academic research. It applies to startups as well.
katiosa 2y ago
This article sort of lists the ideals, but is factually contradicted by the immense amounts of non-impactful and trivial AI papers, who have around 20 authors each. There does seem to be a strong incentive to publish whatever and distribute the credit among dozens of people. For the rare actually impactful research the advice is a bit trivial, you might as well quote Feynman: 1) Sit down. 2) Think hard. 3) Write down the solution.
- abecedarius 2y ago
  Pet peeve: you're quoting not-Feynman.
  - Y_Y 2y ago
    For context, Gell-Mann just said this was how Feynman solved problems, Feynman didn't say it. (Coincidentally it's the same case as the term "Gell-Mann Amnesia".9 https://pca.st/rr17x2vb https://pca.st/rr17x2vb
maleldil 2y ago
"Invest in projects, not papers." is the typical thing you hear from late-stage researchers that forgot what it's like to be a PhD student or early post-doc. We have to publish as much as we can, or our supervisors and committees won't allow us to progress in our careers. I can't spend a year on topics that seem interesting but that might not yield papers if they don't work. From the bureaucratic point of view, which is almost all that matter for junior researchers, that would be simply time in the bin. I would love to spend years on something I care about without caring how many papers it will generate, but if I do that, I won't have a career.
- flobosg 2y ago
  > I won't have a career in academia.
  - anonymoushn 2y ago
    I don't think these big AI labs give you much credit for being a PhD dropout
    - Der_Einzige 2y ago
      They do... if you have NeurIPS/ACL/EMNLP publications! :)
      - maleldil 2y ago
        Even then, there are too many PhDs for few spots in academia and top-tier labs, so there's no way a PhD dropout could compete unless they have some other kind of experience. Also, it's not that hard to publish in high-end NLP conferences, so it doesn't say much.
        Der_Einzige 2y ago
        I watched a startup give an NLP AI engineer with only 1 workshop paper at ACL get a 150K remote offer less than a month ago. This person is in the middle of their BS program right now. It is most certainly not easy to publish top AI research (unless you are doing unethical things). I repeat, if you have a NeurIPS main conference publication, you don't need to have a degree for a top AI lab to at least consider you. If your experiences are different, my guess is that you're not an American.
red_admiral 2y ago
A lot to like here, a couple of things to comment on: > "If you tell people that their systems could be 1.5x faster or 5% more effective, that's rarely going to beat inertia. In my view, you need to find problems where there's non-zero hope that you'll make things, say, 20x faster or 30% more effective, at least after years of work." This works for up-and-coming fields, but once something is stable and works at large scale, it's all about the small improvements. Making petrol engines 1% more fuel-efficient would be massive. Increasing the conversion rate of online ads by 1% could make you very, very rich indeed. Good advice for AI probably; bad advice in other fields. > "Invest in projects, not papers" The best way I think you can go about this is allocate some fraction alpha of your time to projects, and (1-alpha) to things that produce short-term papers. Alpha should never be zero if you want a career, but it will start out small as you begin your PhD and gradually grow, if you can make it in academia. At some point you'll reach a compounding return where the projects themselves are spawning papers - one way to do this is to get to the point where you can hire your own PhD students, but there are several others. As long as your 2-years-into-a-PhD review as some unis have them is about how many papers you've published (somehow weighted by journal/conference rank) and how many others are in the pipeline, you need to focus on papers until the point when your institution will let you do something more useful. Think of it as paper writing bootcamp so that once you do get more time for projects, you'll have practiced how to write up your results. > "Make your release usable, useful ..." This is excellent advice, also for anything else related to code.
- light_hue_1 2y ago
  > Making petrol engines 1% more fuel-efficient would be massive. Increasing the conversion rate of online ads by 1% could make you very, very rich indeed. Good advice for AI probably; bad advice in other fields. It's good advice in every field. Most improvements have a cost. If you make engines 1% more efficient but 5% more expensive no one will care. Heck electric engines are wildly more efficient (80-95%) compared to combustion engines (20-35%), not to mention far simpler, and we can hardly get people to switch. Even immense improvements can be hard to roll out. Don't work on marginal gains. Any minor problem or inconvenience will wipe them out and all your time and effort will be worth nothing. Let people who are paid by companies do that. If you're going to do a PhD focus on something that could be big. Whenever students suggest a project I always start by asking what the upside is: what if we massively succeed?
light_hue_1 2y ago
A lot of the advice is good but this is sad: > First, the problem must be timely. You can define this in many ways, but one strategy that works well in AI is to seek a problem space that will be 'hot' in 2-3 years but hasn't nearly become mainstream yet. I think about research as, what can I bring that's unique? What can I work on that won't be popular or won't exist unless I do it? If it's clearly going to become popular than other people will do it. So why do I need to? I'm useless. Yes. You'll increase your citation count with that plan. But if you're going to do what other people are doing go to industry and make money. It seems crazy to me to give up half a million dollars a year to do something obvious and boring a few months before someone else would do it.
Freedom5093 2y ago
Is this article roughly the application of the startup mindset to research? With the major downsides that you're giving away your insights for free, and potentially actively help other companies profit from your work. You don't go as far as to productize the research, but just make it really easy for others to do so by building "artifacts" for it. I'm not a researcher, but have thought about doing a PhD in the past. It's probably a lot more nuanced that this. Show progress but don't make it easily accessible. *Hide* something important for yourself. Kind of like modern day "open source".
- staunton 2y ago
  > Is this article roughly the application of the startup mindset to research? Somewhat but a few crucial points are missing for it to be that. For example, - hire a lot more people (PhD candidates, postdocs) than you have funding to pay till they finish. Keep growing and getting more grants until you get a Nobel prize (or equivalent) or go broke - fake your data and publish in the top journals/conferences - don't do any research yourself, just get others to do everything and "coordinate" them. Make sure you get all the credit for the publication. The way to get others to do things is to "collaborate" with them or maybe (promise to) pay them.
  - bonoboTP 2y ago
    Once you got that ball rolling your name becomes a "brand" and collaborators will beg you to put your name on their papers so it gets more exposure.
- bonoboTP 2y ago
  This used to be very common but nowadays it's more and more expected to release the code with the paper. This makes it harder to obfuscate big parts of the method. Arguably, this also has lowered the bar for doing incremental research. Just get the code of the sota from github, implement a new feature, test it, if it's 1% better then publish it. Previously there was a natural gatekeep ing effect that you had to be able to understand and translate to code all the math and equations in the paper and be familiar with the dark knowledge details that everyone in the field knows but isn't spelled out explicitly in the papers. Boring bits like how to exactly preprocess, normalize, clean the data, how to precisely do the evals etc.
photochemsyn 2y ago
Academic research in the USA today is entirely corporatized. Try publishing a paper on fine-tuning LLMs with the goal of creating agents capable of replacing the executive suite and the board of directors for major corporations and see what happens to your career. It's far worse today than what Eisenhower described c. 1960 in his final address to the nation, because so much of the research money is now doled out by corporate entities: > "Today, the solitary inventor, tinkering in his shop, has been overshadowed by task forces of scientists in laboratories and testing fields. In the same fashion, the free university, historically the fountainhead of free ideas and scientific discovery, has experienced a revolution in the conduct of research. Partly because of the huge costs involved, a government contract becomes virtually a substitute for intellectual curiosity. For every old blackboard there are now hundreds of new electronic computers. The prospect of domination of the nation's scholars by Federal employment, project allocations, and the power of money is ever present — and is gravely to be regarded." Unless you are independently (very) wealthy, you'll have to align your research with the goals of the funding entity, be that the corporate sector or a government entirely controlled by the corporate sector. You may find something useful and interesting to do within these constraints - but academic freedom is a myth under this system.
- staunton 2y ago
  > Try publishing a paper on fine-tuning LLMs with the goal of creating agents capable of replacing the executive suite and the board of directors for major corporations and see what happens to your career. I expect if you manage to get some interesting results, your career will be great. The trouble is that there aren't any "official" benchmarks for evaluating performance for such a model. That's the main problem and makes it very hard to show if your models are any good.
winar 2y ago
Is there any open-source project recommended that be kind to deep learning newbies that can learn or contribute to?
monicaaa 2y ago
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ethelrugene 2y ago
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lorddr 2y ago
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255 points by KraftyOne 2y ago

This has good advice about academic research in general not just AI Research. It's huge to "Select timely problems with large headroom and "fanout"" - you need a research program to have a successful research career. At least most people do. It's also huge to "Put your work out there and own popularizing your ideas" - the second part is hard for a lot of academics to do. Putting your work out there is huge to get feedback, which may help you pivot or try different directions, as well as fostering collaboration. Collaboration is a large part of being a successful researcher.

Loic 2y ago
> Collaboration is a large part of being a successful researcher. I would even consider it as the largest part. It brings ideas, funding, spreading of your ideas, access to institutional research grants/projects, industry contacts, and more.
- Blahah 2y ago
  Agreed! It also brings friendships, new ways of thinking and framing, inspiration, and the opportunity to give and receive support - to discover how much you can matter, and the good you can do.
  - dkga 2y ago
    Completely second that and the parent comment! Not to mention it’s a good way to have an excuse for a glass of champagne or wine when you finally meet remote co-authors.
- space_oddity 2y ago
  The lifeblood of a successful research career.
vaylian 2y ago
> you need a research program What is a "research program"?
- throw_pm23 2y ago
  the "concepts of a plan"
- antognini 2y ago
  The idea is that rather than doing a bunch of completely independent research projects, all of your projects are designed in service of answering some larger research question.
deleted 2y ago
[deleted]
space_oddity 2y ago
I think many great ideas never gain traction simply because they weren’t communicated effectively

tony_cannistra 2y ago

"Invest in projects, not papers." This is excellent advice, and in my experience does not represent the intuition that many young (and not so young) researchers begin with. Papers come from projects and, if you care, good projects can yield many good papers!

juujian 2y ago
Idk, nothing wrong with going for a low-hanging fruit and doing a one-off sometimes. So many academics fail to get stuff over the finish line. Not the right advice for everybody.
- danielmarkbruce 2y ago
  Interesting. This is a common problem in academia?
  - juujian 2y ago
    Depends on the person. Not unheard of to see people with 10+ working papers that realistically will never see the light of day. Each of those are months of work.
    - danielmarkbruce 2y ago
      I can see that I guess. Easier to start a new one than do the annoying parts to finish one.
- stavros 2y ago
  Yeah, but it's not saying "don't do papers", it's saying your long-term investment should be projects.
- tony_cannistra 2y ago
  nothing wrong except that it might be a distraction, which sometimes is good and sometimes would be better avoided.

vouaobrasil 2y ago

> how do I do research that makes a difference in the current, rather crowded AI space? I hope they are first asking, to which bank accounts is the research actually making a difference? It's a great fraud to present research problems to stimulate the intellect of the naive youth when they have no capability to assess its social impact.

deleted 2y ago
[deleted]

KuriousCat 2y ago

I would say follow the money, create a product or service that generates recurrent income and channel that income to study the fundamental problems that would interest you. Owning a product or platform opens up for a lot of opportunities.

Ar-Curunir 2y ago
Thankfully research is not guided by notions like "what makes money in the current economy"; otherwise we'd be stuck with faster calculators instead of, well, all of modern computer science.
- Maxatar 2y ago
  Most research I know about in academia is absolutely about what makes money.
  - Ar-Curunir 2y ago
    Care to give some examples? It is largely untrue in CS academia, and definitely untrue in every other non-engineering field.
- KuriousCat 2y ago
  I did not say anything about making money in the current economy. Research requires funding and only way to have academic freedom is to have a steady source of recurrent income or funding. One way to get that is to please those who have money but give up part of your control on what you study. Other way is to monetize your knowledge and acquire a ton of money. You seem to misunderstand what I said or have very little clue on how the academia works.
- godelski 2y ago
  > Thankfully research is not guided by notions like "what makes money in the current economy" Unfortunately I don't believe this is true for AI research... I think you'll find a strong correlation with each year's most cited papers and what's currently popular in industry. There's always exceptions, but we moved to a world where we're highly benchmark oriented, and that means we're highly reliant on having large compute infrastructures, and that means that the access and/or funding comes from industry. Who is obviously going to pressure research directions towards certain things.

Der_Einzige 2y ago

At least some of it comes from "hype" too. The author of Dspy (the writer) (https://github.com/stanfordnlp/dspy https://github.com/stanfordnlp/dspy) should know this, given that Dspy is nothing more than fancy prompts optimizing prompts to be fancier according to prompt chains described in papers (i.e. Chain of thought, Tree of thought, etc). Textgrad (https://github.com/zou-group/textgrad https://github.com/zou-group/textgrad) is an even worse example of this, as it makes people think that it's not just a prompt optimizing another prompt Dspy has 17k stars, meanwhile PyReft (https://github.com/stanfordnlp/pyreft https://github.com/stanfordnlp/pyreft) isn't even at 1200 yet and it has Christopher Manning (head of AI at stanford) working on it (see their paper: https://arxiv.org/abs/2404.03592 https://arxiv.org/abs/2404.03592). Sometimes what the world deems "impactful" in the short-medium term is wrong. Think long term. PyReft is likely the beginning of an explosion in demand for ultra parameter efficient techniques, while Dspy will likely fade into obscurity over time. I also know that the folks writing better samplers/optimizers for LLMs get almost no love/credit relative to the outsized impact they have on the field. A new sampler potentially improves EVERY LLM EVER! Folks like Clara Meister or the authors of the min_p paper preprint have had far larger impacts on the field than their citation counts might suggest, based on the fact that typiciality or min_p sampling is now considered generally superior to top_p/top_k (OpenAI, Anthropic, Gemini, et al still use top_p/top_k) and min_p/typicality are implemented by every open source LLM inference engine (i.e. huggingface, vllm, sglang, etc)

thelastbender12 2y ago
I think that's a little harsh. Imo the reason for difference in popularity/github-stars is just different user bases- an order of magnitude more people use LLM APIs (and can leverage Dspy) vs those who finetune an LLM. Agree about the abstractions btw. I found Dspy very convoluted for what it does, couldn't make sense of Textgrad at all.

sashank_1509 2y ago

Unfortunately while this advice sounds useful, it isn’t. It might be useful if you measure impact is the fake metrics like citation count but if you want to measure with actual tangible impact on the real world, you have a rude awakening before you. To me there are 2 ways a paper can create impact: 1. The paper represents such an impressive leap in performance over existing methods in AI, that it is obviously impactful. Unfortunately, this way of generating impact is dominated by industry. No one can expect Academia to train O1, SAM, GPT5 etc. AI rewards scale, scale requires money, resources and manpower and Academia has none. In the early days of AI, there were rare moments when this was possible, AlexNet, Adam, Transformers, PPO etc. Is it still possible? I do not know, I have not seen anything in the last 3 years and I’m not optimistic many such opportunities are left. Even validating your idea tends to require the scale of industry. 2. The paper affects the thought process of other AI researchers and thus you are indirectly impactful if any of them cause big leaps in AI performance. Unfortunately here is where Academia has shot itself in the foot by generating so many damn papers every year (>10,000). There are just so many, that the effect of any 1 paper is meaningless. In fact the only way to be impactful now is to be in a social circle of great researchers, so that you know your social circle will read your paper and later if any of them make big performance improvements, you can believe that you played a small role in it. I have spoken to a lot of ML researchers, and they told me they choose papers to read just based on people and research groups they know. Even being a NeurIPS spotlight paper, means less than 10% of researchers will read your paper, maybe it will go to 50% if it’s a NEURIPS best paper but even that I doubt. How many researchers remember last year’s NEURIPS best paper? The only solution to problem 2, is radical. The ML community needs to come together and limit the number of papers it wide releases. Let us say it came out and said that yearly only 20 curated papers will be widely published. Then you can bet most of the ML community will read all 20 of those papers and engage with it deeply as they will be capable of spending more than a day at least thinking about the paper. Of course you can still publish on arxiv, share with friends etc but unless such a dramatic cutdown is made I don’t see how you can be an actually impactful AI researcher in Academia when option 1 is too expensive and option 2 is made impossible.

EnigmaFlare 2y ago
If you were a really good academic, you could come up with a theory that predicts the performance of a model you haven't actually tested. Physics is full of this - theories that predict something novel followed by other people doing expensive experiments to test them. The guy who published the theory gets the credit. That's probably what we want from academic AI researchers - theories that we can eventually use to design models, rather than just haphazardly building something and wondering how good it will be.

lmeyerov 2y ago

I like the article directionally but fear the examples are too short-sighted for most AI researchers. Picking something useful in 1-2 years is a reason to go to industry, not research, and leads to mostly incremental units that if you don't do, someone else will. Yes, hot topics are good because they signal a time of fertile innovation. But not if your vision is so shallow that you will have half of IBM, Google, and YC competing with you before you start or by the time of your first publication (6-12mo). If you are a top student, well-educated already, with top resources and your own mentees, and your advisor is an industry leader who already knows where your work will go, maybe go to the thickest 1-2 year out AI VC fest, but that's not most PhD students. A 'practical' area would be obvious to everyone in 5 years, but winnowing out the crowd, there should not be much point to it today nor 1-2 years without something fundamentally changing. It should be tangible enough to be relevant and enticing, but too expensive for whatever reasons. More fundamental research would be even more years out. This gives you a year or two to dig into the problem, and another year or two to build out fundamental solutions, and then a couple years of cranking. From there, rinse-and-repeat via your own career or those of your future students. Some of my favorite work took 1-2 years of research to establish the problem, not just the solutions. Two of the projects here were weird at first as problems on a longer time scale, but ended up as part of $20M grant and software many folks here use & love, and another, a 10 year test of time award. (And another, arguably a $100M+ division at Nvidia). In contrast, most of my topic-of-the-year stuff didn't matter and was interchangeable with work by others. Edit: The speech by Hamming on "You and your research" hits on similar themes and speaks more to my experiences here: https://fs.blog/great-talks/richard-hamming-your-research/ https://fs.blog/great-talks/richard-hamming-your-research/

QuadmasterXLII 2y ago
If no one did the research that anyone could do, it would never get done.
- marcosdumay 2y ago
  In most markets, it pays to be contrarian. ... and when everybody decides to be a contrarian, the contrarian position is to do the popular thing. But the catch is that this never happens on practice.

spatalo 2y ago

i don't fully agree with the headroom, many papers were published achieving 1% improvement on ImageNet...

Nevermark 2y ago
Agreed. Any improvement in a well established and competitive metric which a community is tracking is going to get attention and respect.

low_tech_love 2y ago

Although point #1 is true, I find it to be a slightly superficial advice. It's like saying "if you want to be happy, find a job that fulfills you". Sure, everyone wants to be able to focus on good projects before papers, so that the papers come naturally. If you can do that, congrats! You won the game; be proud and enjoy it. However, the truth is that the way to get there is dark and lonely and full of terrors, and not everyone can do it. All academics (especially junior ones) are constantly in the middle of an ambiguous, contradictory discourse: you must produce a lot, but you also must produce high-quality output. Your environment, literally everyone around you, wants to have your cake and eat it too. As you get more experienced you learn to navigate this and keep the good parts while ignoring the bad ones, but for young researchers this can be extremely taxing and stressful. In order to "focus on projects and not papers" you have to literally swim against the current, usually in a very very strong current. Not everyone has the presence of mind and attitude to do it, and to be honest, it's not fair to expect that either. So, here are some points and comments I offer that go in a slightly different direction (although, like I said, if you managed to get there, congrats!): * You can write a good paper without it being a good project. One thing does not exclude the other, and the fact that there are many bad papers out there does not mean that papers themselves are bad. You can plan your work around a paper, do a good research job, and write a good scientific report without having to have an overarching research project that spills over that. Sure, it is great when it happens (and it will happen the more experienced and senior you get), but it's not necessarily true. * Not thinking about the paper you'll write out of your work might deter you from operationalizing your research correctly. Not every project can be translated into a good research paper, with objective/concrete measurements that translate to a good scientific report. You might end up with a good Github repo (with lots of stars and forks) and if that's your goal, then great! But if your goal is to publish, you need to think early on: "what can I do that will be translated into a good scientific paper later?" This will guide your methods towards the right direction and make sure you do not pull your hair later (at least not as many) when you get rejected a million times and end up putting your paper in a venue you're not proud of. * Publishing papers generates motivation. When a young research goes too long without seeing the results of their work, they lose motivation. It's very common for students to have this philosophical stance that they want to work on the next big project that will change the world, and that they need time and comfort and peace to do that, so please don't bother me with this "paper" talk. Fast forward three years later they have nothing published, are depressed, and spend their time playing video games and procrastinating. The fact is that people see other people moving forward, and if they don't, no amount of willpower to "save the world" with a big project will keep them going. Publishing papers gives motivation; you feel that your work was worth it, you go to conferences and talk to people, you hear feedback from the community. It's extremely important, and there's no world where a PhD student without papers is healthier and happier than one with papers. * Finishing a paper and starting the next one is a healthy work discipline. Some people just want to write a good paper and move on. Not everyone feels so passionate about their work that they want to spend their personal time with it, and push it over all boundaries. You don't have to turn your work into your entire life. Doing a good job and then moving on is a very healthy practice.

mehulashah 2y ago

This advice is much more general than academic research. It applies to startups as well.

katiosa 2y ago

This article sort of lists the ideals, but is factually contradicted by the immense amounts of non-impactful and trivial AI papers, who have around 20 authors each. There does seem to be a strong incentive to publish whatever and distribute the credit among dozens of people. For the rare actually impactful research the advice is a bit trivial, you might as well quote Feynman: 1) Sit down. 2) Think hard. 3) Write down the solution.

abecedarius 2y ago
Pet peeve: you're quoting not-Feynman.
- Y_Y 2y ago
  For context, Gell-Mann just said this was how Feynman solved problems, Feynman didn't say it. (Coincidentally it's the same case as the term "Gell-Mann Amnesia".9 https://pca.st/rr17x2vb https://pca.st/rr17x2vb

maleldil 2y ago

"Invest in projects, not papers." is the typical thing you hear from late-stage researchers that forgot what it's like to be a PhD student or early post-doc. We have to publish as much as we can, or our supervisors and committees won't allow us to progress in our careers. I can't spend a year on topics that seem interesting but that might not yield papers if they don't work. From the bureaucratic point of view, which is almost all that matter for junior researchers, that would be simply time in the bin. I would love to spend years on something I care about without caring how many papers it will generate, but if I do that, I won't have a career.

flobosg 2y ago
> I won't have a career in academia.
- anonymoushn 2y ago
  I don't think these big AI labs give you much credit for being a PhD dropout
  - Der_Einzige 2y ago
    They do... if you have NeurIPS/ACL/EMNLP publications! :)
    - maleldil 2y ago
      Even then, there are too many PhDs for few spots in academia and top-tier labs, so there's no way a PhD dropout could compete unless they have some other kind of experience. Also, it's not that hard to publish in high-end NLP conferences, so it doesn't say much.
      - Der_Einzige 2y ago
        I watched a startup give an NLP AI engineer with only 1 workshop paper at ACL get a 150K remote offer less than a month ago. This person is in the middle of their BS program right now. It is most certainly not easy to publish top AI research (unless you are doing unethical things). I repeat, if you have a NeurIPS main conference publication, you don't need to have a degree for a top AI lab to at least consider you. If your experiences are different, my guess is that you're not an American.

red_admiral 2y ago

A lot to like here, a couple of things to comment on: > "If you tell people that their systems could be 1.5x faster or 5% more effective, that's rarely going to beat inertia. In my view, you need to find problems where there's non-zero hope that you'll make things, say, 20x faster or 30% more effective, at least after years of work." This works for up-and-coming fields, but once something is stable and works at large scale, it's all about the small improvements. Making petrol engines 1% more fuel-efficient would be massive. Increasing the conversion rate of online ads by 1% could make you very, very rich indeed. Good advice for AI probably; bad advice in other fields. > "Invest in projects, not papers" The best way I think you can go about this is allocate some fraction alpha of your time to projects, and (1-alpha) to things that produce short-term papers. Alpha should never be zero if you want a career, but it will start out small as you begin your PhD and gradually grow, if you can make it in academia. At some point you'll reach a compounding return where the projects themselves are spawning papers - one way to do this is to get to the point where you can hire your own PhD students, but there are several others. As long as your 2-years-into-a-PhD review as some unis have them is about how many papers you've published (somehow weighted by journal/conference rank) and how many others are in the pipeline, you need to focus on papers until the point when your institution will let you do something more useful. Think of it as paper writing bootcamp so that once you do get more time for projects, you'll have practiced how to write up your results. > "Make your release usable, useful ..." This is excellent advice, also for anything else related to code.

light_hue_1 2y ago
> Making petrol engines 1% more fuel-efficient would be massive. Increasing the conversion rate of online ads by 1% could make you very, very rich indeed. Good advice for AI probably; bad advice in other fields. It's good advice in every field. Most improvements have a cost. If you make engines 1% more efficient but 5% more expensive no one will care. Heck electric engines are wildly more efficient (80-95%) compared to combustion engines (20-35%), not to mention far simpler, and we can hardly get people to switch. Even immense improvements can be hard to roll out. Don't work on marginal gains. Any minor problem or inconvenience will wipe them out and all your time and effort will be worth nothing. Let people who are paid by companies do that. If you're going to do a PhD focus on something that could be big. Whenever students suggest a project I always start by asking what the upside is: what if we massively succeed?

light_hue_1 2y ago

A lot of the advice is good but this is sad: > First, the problem must be timely. You can define this in many ways, but one strategy that works well in AI is to seek a problem space that will be 'hot' in 2-3 years but hasn't nearly become mainstream yet. I think about research as, what can I bring that's unique? What can I work on that won't be popular or won't exist unless I do it? If it's clearly going to become popular than other people will do it. So why do I need to? I'm useless. Yes. You'll increase your citation count with that plan. But if you're going to do what other people are doing go to industry and make money. It seems crazy to me to give up half a million dollars a year to do something obvious and boring a few months before someone else would do it.

Freedom5093 2y ago

Is this article roughly the application of the startup mindset to research? With the major downsides that you're giving away your insights for free, and potentially actively help other companies profit from your work. You don't go as far as to productize the research, but just make it really easy for others to do so by building "artifacts" for it. I'm not a researcher, but have thought about doing a PhD in the past. It's probably a lot more nuanced that this. Show progress but don't make it easily accessible. *Hide* something important for yourself. Kind of like modern day "open source".

staunton 2y ago
> Is this article roughly the application of the startup mindset to research? Somewhat but a few crucial points are missing for it to be that. For example, - hire a lot more people (PhD candidates, postdocs) than you have funding to pay till they finish. Keep growing and getting more grants until you get a Nobel prize (or equivalent) or go broke - fake your data and publish in the top journals/conferences - don't do any research yourself, just get others to do everything and "coordinate" them. Make sure you get all the credit for the publication. The way to get others to do things is to "collaborate" with them or maybe (promise to) pay them.
- bonoboTP 2y ago
  Once you got that ball rolling your name becomes a "brand" and collaborators will beg you to put your name on their papers so it gets more exposure.
bonoboTP 2y ago
This used to be very common but nowadays it's more and more expected to release the code with the paper. This makes it harder to obfuscate big parts of the method. Arguably, this also has lowered the bar for doing incremental research. Just get the code of the sota from github, implement a new feature, test it, if it's 1% better then publish it. Previously there was a natural gatekeep ing effect that you had to be able to understand and translate to code all the math and equations in the paper and be familiar with the dark knowledge details that everyone in the field knows but isn't spelled out explicitly in the papers. Boring bits like how to exactly preprocess, normalize, clean the data, how to precisely do the evals etc.

photochemsyn 2y ago

Academic research in the USA today is entirely corporatized. Try publishing a paper on fine-tuning LLMs with the goal of creating agents capable of replacing the executive suite and the board of directors for major corporations and see what happens to your career. It's far worse today than what Eisenhower described c. 1960 in his final address to the nation, because so much of the research money is now doled out by corporate entities: > "Today, the solitary inventor, tinkering in his shop, has been overshadowed by task forces of scientists in laboratories and testing fields. In the same fashion, the free university, historically the fountainhead of free ideas and scientific discovery, has experienced a revolution in the conduct of research. Partly because of the huge costs involved, a government contract becomes virtually a substitute for intellectual curiosity. For every old blackboard there are now hundreds of new electronic computers. The prospect of domination of the nation's scholars by Federal employment, project allocations, and the power of money is ever present — and is gravely to be regarded." Unless you are independently (very) wealthy, you'll have to align your research with the goals of the funding entity, be that the corporate sector or a government entirely controlled by the corporate sector. You may find something useful and interesting to do within these constraints - but academic freedom is a myth under this system.

staunton 2y ago
> Try publishing a paper on fine-tuning LLMs with the goal of creating agents capable of replacing the executive suite and the board of directors for major corporations and see what happens to your career. I expect if you manage to get some interesting results, your career will be great. The trouble is that there aren't any "official" benchmarks for evaluating performance for such a model. That's the main problem and makes it very hard to show if your models are any good.

winar 2y ago

Is there any open-source project recommended that be kind to deep learning newbies that can learn or contribute to?

monicaaa 2y ago

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