There is an odd belief perpetuated in the machine learning community that massive compute and "big data" represent obstacles that are nearly impossible to scale. They're not. We've defeated those obstacles time and time again.
Over time the roaring waterfall fades back into a quiet stream.
Headlines and hype misrepresent the true pace of progress. Numbers are thrown around either as vanity metrics or as a result of misunderstanding how efficiently a task might be solved. What is possible has not yet been well defined.
Our community has an ongoing defeatist narrative whilst every year more and more David v Goliath stories are fought, won, and somehow promptly forgotten. Isolate what matters in the long term from what gets the spotlight at this moment. This is a good general life principle and an especially strong guiding principle for sanity in your own work when the field is full of question marks.
Irrational courage is a skill worth cultivating. Why? It may be irrational in the face of the community yet entirely rational in reality. When I was at university neural networks themselves were dismissed as [insane, stupid, wasteful, fanciful, only capable of "local optimimums"] and should therefore be forgetten. Reality took a long time (and many courageous souls) before that perception was overturned. What else is left to discover on the discarded fringes of impossible adjacent?
For machine learning, history has shown compute and data advantages rarely matter in the long run. The ongoing trends indicate this will only become more true over time than less. You can still contribute to this field with limited compute and even data. It is especially true that you can get almost all the advances of the field with limited compute and data. Those limits may even be to your advantage.
Is this true for every application? No. Yet I genuinely believe it true in most cases.
Note: If you're interested in following this line of thought my earlier article Backing off towards simplicity - why baselines need more love presents a process you can follow for research or implementation.
Preface: None of what I note below means massive compute is bad, either in research or implementation. Massive compute frequently results in insight that feed our understanding of later techniques, showing either the full possibility or limits even at tremendous scale. Massive compute rarely results in efficiency gains by itself.
Excess compute frequently ends up as a crutch, not a breakthrough. Over time the march of hardware, the march of techniques, and our improved understanding trim away the excess where it isn't needed.
Adding ever more engines may help get the plane off the ground...
but that's not the design planes are destined for.
Two extremes of this trend to be considered:
New York Times (2012): "How Many Computers to Identify a Cat? 16,000 (CPU cores)"
One year later: "three servers each with two quad-core CPUs and four Nvidia GeForce GTX 680 GPUs"
Neural Architecture Search: "32,400-43,200 GPU hours"
Just over a year later: "single Nvidia GTX 1080Ti GPU, the search for architectures takes less than 16 hours" (1000x less) (paper)
Whilst there are many many more examples of this trend I could note, a rule of thumb is:
What may take a cluster to compute one year takes a consumer machine the next.
Is this overly optimistic? Sure. I would argue that it is less wrong than "what took a cluster to compute one year takes a cluster to compute the next" however. Even if it's wrong it's better than our current thinking that may paralyze us with fear rather than exploring what is or isn't possible. Just like Moore's law it may prove a better target for progress than a fundamental law in and of itself.
There is a traditional notion that data moats are impossible to cross. In some fields data moats do indeed still hold strong yet the overall trend is that intelligently used small data is better than big data. Even better, the size requirement for annotated data is continuously falling, meaning annotated data moats are also falling away.
The largest trend here is unsupervised sequence modeling. What went from an uncool and "useless" little task (language modeling) is now proving to be NLP's ImageNet moment. A similar trend is following in vision and many other domains. Understanding a smaller dataset in detail proves far more useful than a large dataset ("big data") with unintelligent methods. Quite literally, only two or so years ago, language modeling papers were a hard sell at conferences. Why? People beleived them to be of limited use and essentially an insular and unimpactful subcommunity. Time and the people within that silly little subfield proved the task's worth.
I will give an example below but writing in more detail is beyond scope - mainly as I may never get this article out the door otherwise. If you're interested in my thoughts, message me, and I'll add it to my writing queue!
I have lost months of my life taunted and terrified by massive compute. Literally. They were the darkest days of my research career. A stage where I felt the walls closing in and the billions of FLoPs that I had access to but a tap trying to fill a river.
My focus had been on language modeling. I'd published one strong paper on it - Pointer Sentinel Mixture Models - and a team at Facebook had developed a similar idea independently in parallel with a brilliant speed gain over my work! I was so happy. I was on the parallel cutting edge, exploring ideas that others found value in.
Then Neural Architecture Search with Reinforcement Learning came out, blowing my results out of the water. I spent months trying to replicate the work. Part of the issue was missing details in the paper - but every paper has missing details. That's the standard life of a researcher. The other far more pressing issue was that I'd convinced myself that Neural Architecture Search and the many GPUs it used was necessary for that level of performance. This was not true.
Under this misguided notion, I scaled my GPUs from the single GPU I had to many. Far too many. I eventually commanded an armada of 40 GPUs. I was trying to use them efficiently, believing there was a better and saner way to the same results, but I was met with obstacles at nearly every turn. I was sticky taping a distributed solution together that slowed my thinking down and distracted me from the core task. Whilst I gained many insights from that eventual work (mainly thanks to Martin Schrimpf for replacing the sticky tape with sound engineering), much of the work I put into the project proved an utter distraction for me.
Upon submitting the paper I conceded defeat in my mind. I decided to move away from language modeling and try my hand elsewhere. My lovely subfield was going where I could not follow.
As a swansong I decided to improve the PyTorch language modeling example. I always had a sweetspot for good tutorial code and it had proven helpful for my initial implementation. I wanted to give back and give anyone who followed me the best fighting chance possible. I decided to only improve the model in ways that were fast as the end user needed to be able to explore and tinker sanely on any GPU.
To my surprise the simple improvement I made got the model to soar. I removed a small bit of cruft and found the aerodynamic drag disappeared. A single modest GPU was beating out all past work in hours. The side project of improving a tutorial ended up relighting my passion and confidence in competing in my own field. Brilliant colleagues joined me to bring the work from a surprise proof of concept to the final string of papers.
In parallel and independently a brilliant team at DeepMind/University of Oxford realized many of the same efficiency gains (and a far more nuanced analysis) in On the State of the Art of Evaluation in Neural Language Models. I am glad for that. Even if I had conceded defeat and never discovered my flawed thinking by chance I would have when they finally published. By this stage I had lost months however - and nearly lost my internal drive.
Before the new fangled neural language models or even the resurgence of the neural network era, my obsession was with n-grams. They're the simplest things in the world. Take N words - let's say these five words right here. That's a five-gram. Imagine seeing all the possible five-grams on earth.
If you collect all the occurrences of these n-grams, you gain insight into how words are used. Working out the next word in The distance from Sydney to New ____ is easy - find all five grams starting with "from Sydney to New"! Want to know flavours are available? Find all the patterns where people are ordering ice cream and extract!
The issue is that there are exponentially increasing n-grams as you increase the value of n. If you have a vocabulary of 10,000 then there are 10,000^2 potentially 2-grams, 10,000^3 potential 3-grams, and so on. You need ever more data to try to capture these patterns.
Google released an n-gram dataset that was enormous at the time. 24 gigabytes compressed - oh geez! Solid state disks weren't a thing and RAM was, as ever, far too few, especially for holding a dataset of that size just for random access.
I pondered how to attach dozens or hundreds of USBs - the only sanely cheap solid state disk at the time - through an ever growing vine of USB hubs. This taught me a great deal about the lower levels of compute and storage but it didn't help me solve the task itself.
Today, with a tiny slither of the data used to produce n-grams or even store the original n-gram dataset, a single desktop computer can give you a richer representation in under an hour. How? More efficient usage of the data. That was the word2vec and eventually unsupervised language modeling path.
I don't want others to lose months of their time or neurons of their sanity like I have done in the past. It's not necessary. It's not productive. It's rarely what you need to achieve your aims or to help forge progress in our field.
There's need for courage to push beyond what others tell you is possible. Most of the time what's possible hasn't been properly defined yet.
Interested in saying hi? ^_^