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Research Directions for Machine Learning and Algorithms

Muthu invited me to the workshop on algorithms in the field, with the goal of providing a sense of where near-term research should go. When the time came though, I bargained for a post instead, which provides a chance for many other people to comment.

There are several things I didn’t fully understand when I went to Yahoo! about 5 years ago. I’d like to repeat them as people in academia may not yet understand them intuitively.

  1. Almost all the big impact algorithms operate in pseudo-linear or better time. Think about caching, hashing, sorting, filtering, etc… and you have a sense of what some of the most heavily used algorithms are. This matters quite a bit to Machine Learning research, because people often work with superlinear time algorithms and languages. Two very common examples of this are graphical models, where inference is often a superlinear operation—think about the n2 dependence on the number of states in a Hidden Markov Model and Kernelized Support Vector Machines where optimization is typically quadratic or worse. There are two basic reasons for this. The most obvious is that linear time allows you to deal with large datasets. A less obvious but critical point is that a superlinear time algorithm is inherently buggy—it has an unreliable running time that can easily explode if you accidentally give it too much input.
  2. Almost anything worth doing requires many people working together. This happens for many reasons. One is the time-critical aspect of development—in many places it really is worthwhile to pay more to have something developed faster. Another is that real projects are simply much bigger than you might otherwise expect. A third is that real organizations have people coming and going, and any project that is just by one person whithers when they leave. This observation is what means that development of systems with clean abstractions can be extraordinarily helpful, as it allows people to work independently. This observation also means that simple widely applicable tricks (for example the hashing trick) can be broadly helpful.

A good way to phrase research directions is with questions. Here are a few of my natural questions.

  1. How do we efficiently learn in settings where exploration is required? These are settings where the choice of action you take influences the observed reward—ad display and medical testing are two good scenarios. This is deeply critical to many applications, because the learning with exploration setting is inherently more natural than the standard supervised learning setting. The tutorial we did details much of the state of the art here, but very significant questions remain. How can we do efficient offline evaluation of algorithms (see here for a first attempt)? How can we be both efficient in sample complexity and computational complexity? Several groups are interested in sampling from a Bayesian posterior to solve these sorts of problems. Where and when can this be proved to work? (There is essentially no analysis.) What is a maximally distributed and incentive compatible algorithm that remains efficient? The last question is very natural for market place design. How can we best construct reward functions operating on different time scales? What is the relationship between the realizable and agnostic versions of this setting, and how can we construct an algorithm which smoothly interpolates between the two?
  2. How can we learn from lots of data? We’ll be presenting a KDD survey tutorial about what’s been done. Some of the larger scale learning problems have been addressed effectively using MapReduce. The best example here I know is known as Ozgur Cetin’s algorithm at Y!—It’s preconditioned conjugate gradient with a Newton stepsize using two passes over examples per step. (A nonHadoop version is implemented in VW for reference.) But linear predictors are not enough—we would like learning algorithms that can for example learn from all the images in the world. Doing this well plausibly requires a new approach and new learning algorithms. A key observation here is that the bandwidth required by the learning algorithm can not be too great.
  3. How can we learn to index efficiently? The standard solution in information retrieval is to evaluate (or approximately evaluate) all objects in a database returning the elements with the largest score according to some learned or constructed scoring function. This is an inherently O(n) operation, which is frustrating when it’s plausible that an exponentially faster O(log(n)) solution exists. A good solution involves both theory and empirical work here, as we need to think about how to think about how to solve the problem, and of course we need to solve it.
  4. What is a flexible inherently efficient language for architecting representations for learning algorithms? Right now, graphical models often get (mis)used for this purpose. It’s easy and natural to pose a computationally intractable graphical model, implying many real applications involve approximations. A better solution would be to use a different representation language which was always computationally tractable yet flexible enough to solve real-world problems. One starting point for this is Searn. Another general approach was the topic of the Coarse to fine workshop. These are inherently related as Coarse to fine is a pruned breadth first search. Restated, it is not enough to have a language for specifying your prior structural beliefs—instead we must have a language for such which results in computationally tractable solutions.
  5. The Deep Learning problem remains interesting. How do you effectively learn complex nonlinearities capable of better performance than a basic linear predictor? An effective solution avoids feature engineering. Right now, this is almost entirely dealt with empirically, but theory could easily have a role to play in phrasing appropriate optimization algorithms, for example.

Good solutions to each of the research directions above would result in revolutions in their area, and everyone of them would plausibly see wide applicability.

What’s missing?

Cross-posted at CACM.

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In Active Learning, the question changes

A little over 4 years ago, Sanjoy made a post saying roughly “we should study active learning theoretically, because not much is understood”.

At the time, we did not understand basic things such as whether or not it was possible to PAC-learn with an active algorithm without making strong assumptions about the noise rate. In other words, the fundamental question was “can we do it?”

The nature of the question has fundamentally changed in my mind. The answer is to the previous question is “yes”, both information theoretically and computationally, most places where supervised learning could be applied.

In many situation, the question has now changed to: “is it worth it?” Is the programming and computational overhead low enough to make the label cost savings of active learning worthwhile? Currently, there are situations where this question could go either way. Much of the challenge for the future is in figuring out how to make active learning easier or more worthwhile.

At the active learning tutorial, I stated a set of somewhat more precise research questions that I don’t yet have answer to, and which I believe are worth answering. Here is a bit of an expansion on those questions for those interested.

  1. Is active learning possible in a fully adversarial setting? By fully adversarial, I mean when an adversary controls all the algorithms observations. Some work by Claudio and Nicolo has moved in this direction, but there is not yet a solid answer.
  2. Is there an efficient and effective reduction of active learning to supervised learning? The bootstrap IWAL approach is efficient but not effective in some situations where other approaches can succeed. The algorithm here is a reduction to a special kind of supervised learning where you can specify both examples and constraints. For many supervised learning algorithms, adding constraints seems problematic.
  3. Can active learning succeed with alternate labeling oracles? The ones I see people trying to use in practice often differ because they can provide answers of varying specificity and cost, or because some oracles are good for some questions, but not good for others.
  4. At this point, there have been several successful applications of active learning, but that’s not the same thing as succeeding with more robust algorithms. Can we succeed empirically with more robust algorithms? And is the empirical cost of additional robustness worth the empirical peace-of-mind that your learning algorithm won’t go astray where other more aggressive approaches may do so?
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Holy grails of machine learning?

Let me kick things off by posing this question to ML researchers:

What do you think are some important holy grails of machine learning?

For example:
– “A classifier with SVM-level performance but much more scalable”
– “Practical confidence bounds (or learning bounds) for classification”
– “A reinforcement learning algorithm that can handle the ___ problem”
– “Understanding theoretically why ___ works so well in practice”
etc.

I pose this question because I believe that when goals are stated explicitly and well (thus providing clarity as well as opening up the problems to more people), rather than left implicit, they are likely to be achieved much more quickly. I would also like to know more about the internal goals of the various machine learning sub-areas (theory, kernel methods, graphical models, reinforcement learning, etc) as stated by people in these respective areas. This could help people cross sub-areas.