Heuristics

Deepak brings up a great discussion topic that really needs its own post. Hopefully I'll catch this here before anyone continues to reply there (don't). The basic question is this:

Why cannot people simply use heuristicy and hackery approaches that have been proven over years to work well?

Deepak's point, which I think is well taken and should not be forgotten, is that a simple "hacky" thing (I don't intend "hacky" to be condescending...Deepak used it first!) often only does at most epsilon worse than a mathematically compelling technique, and sometimes even better. I think you can make a stronger argument. Hacky things allow us to essentailly encode any information we want into a system. We don't have to find a mathematically convenient way of doing so (though things are better now that we don't use generative models for everything).

I think there are several responses to these arguments, but I don't think anything topples the basic point. But before I go into those, I want to say that I think there's a big difference between simple techniques and heuristicy techniques. I am of course in favor of the former. The question is: why shouldn't I just use heuristics. Here are some responses.

1. That's just how I am. I studied math for too long. It's purely a personal choice. This is not compelling on a grand scale, but at a personal level, it is unlikely one will do good research if one is not interested in the topic and approach.
   
2. We don't want to just solve one problem. Heuristic techniques are fantastic for solving a very particular problem. But they don't generalize to other similar problems. The extent to which they don't generalize (or the difficulty to force generalization) of course varies.
3. Similar to #2, I want a technique that can be described more briefly than simply the source code. Heuristic techniques by definition cannot. Why? I'd like to know what's really going on. Maybe there's some underlying principle that can be applied to other problems.
4. Lasting impact. Heuristics rarely have lasting (scientific) impact because they're virtually impossible to reproduce. Of course, a lasting impact for something mathematically clever but worthless is worse than worthless.

There are probably others that other people can come up with.

That's my general perspective. In response to specific issues Deepak brought up:

...a more complicated model gives very little improvements and generally never scales easily.

I think it's worthwhile separating the problem from the solution. The issue with a lot of techniques not scaling is very true. This is why I don't want to use them :). I want to make my own techniques that do scale and that make as few assumptions as possible (regarding features, loss, data, etc.). I think we're on our way to this. Together with John and Daniel, we have some very promising results.

...working on such (SP) problems means getting married more to principles of Machine Learning than trying to make any progress towards real world problems.

I, personally, want to solve real-world problems. I cannot speak for others.

...a lot of lot of smart (young?) people in the NLP/ML community simply cannot admit the fact that simple techniques go a long way...

This is very unfortunate if true. I, for one, believe that simple techniques do go a long way. And I'm not at all in favor of using a steamroller to kill a fly. But I just don't feel like they can or will go all the way in any scalable manner (scalable in O(person time) not O(computation time)). I would never (anymore!) build a system for answering factoid questions like "how tall is the empire state building?" that is not simple. But what about the next level "how much taller is the empire state building than the washington monument?" Okay, now things are interesting, but this is still a trivial question to answer. Google identifies this as the most relevant page. And it does contain the necessary information. And I can imagine building heuristics that could answer "how much Xer is X that Y" based on asking two separate questions. But where does this process end? I will work forever on this problem. (Obviously this is just a simple stupid example which means you can find holes in it, but I still believe the general point.)

Yesterday was Structured Learning Day

I'm out in Chicago at the atomic learning workshop and yesterday was structured prediction day. There were a lot of cool talks on pretty much all the major SP techniques: Charles talked about efficient training of CRFs, Yasemin talked about semi-supervised learning in M3Ns and SVMISOs, Ben talked about efficient training of M3Ns for combinatorial-style problems (like word alignment), Drew talked about planning as a SP problem, Vasin talked about the tradeoffs of local vs. global inference in SP, and I of course talked about search.

I really enjoyed Drew's talk. He is considering the problem of robot navigation, which is typically handled using A* search and some very crafty hand-written heuristic rules for generating the cost map over which A* search runs. He wants to get rid of the crafty part and replace it with learning. The idea is simple and cute: use observed features the robot receives to learn to produce a cost map so that when A* runs it finds the right path. Here, he defines the right path by having a human remote control the robot and drive it to the correct place. He casts this as a max-margin problem and solves it using very fast subgradient methods. There's no paper on this yet, but if all goes well there will be soon. I think there's a lot of stuff here that could strongly influence how we think about SP.

There were many questions raised at the workshop that I deserve significant thought. These include:

1. What is structured learning?
2. How does structured learning related to multi-task learning (ala Rich Caruana and others)?
3. What sort of techniques are there for dealing with un- or partially-labeled data for structured learning?
4. What can be done about featuritis (i.e., throwing in all possible features)? Also: Is this a legitimate concern?
5. How important is it what loss function we optimize?
6. When is local learning enough (ala Dan Roth) and when must you do "global learning?"
7. What training techniques scale sufficiently?

Almost all of these questions deserve separate posts, and of course they are non-independent. Modulo feedback, I'll probably start at the top and work my way down. (Of course, if John beats me to it, I'll just post on his blog and cross-link here.)

Viterbi Search is Not Magic

This post is about the use of Viterbi search in NLP applications. Skip the next paragraph if you recall readily how VS works.

The easiest formulation of VS is for a sequence labeling problem: given an input x, find a label vector y1,...,yN that maximizes the score [ f(x,y0,y1) + f(x,y1,y2) + ... + f(x,y{N-1},yN) ]. (Here, y0 is some special <s> symbol.) When there are K possible values for each label, VS solves this by filling in a dynamic programming matrix a of size (N+1)*K, where a(0,k) is zero if k is <s> and negative infinity otherwise. Recursively, a(n+1,k') is [ max_k [ a(n,k) + f(x,k,k') ] ]. The largest a(N+1, . ) gives the highest score; by storing backpointers (which k was the largest) in another matrix, we can recover the whole sequence once we reach the end. This runs in time O(NK^2), as opposed to O(N^K) as a naive implementation would run.

I am becoming somewhat notorious for not using Viterbi search, even for sequence labeling problems (ironic, given that I am part of the Viterbi School of Engineering). The purpose of this post is to show that this is not unreasonable.

My evolving feeling on this has two angles:

1. Viterbi is good for something like an HMM where we can't model the whole input as features and so we need to talk back-and-forth via Viterbi. But when we get to use any feature at any time (as in any modern model), this advantage goes away.
2. I think people ascribe some "magic" to Viterbi. At least in NLP, the Viterbi algorithm and its generalizations (inside-outside, etc.) are treated as stand alone units. They're not. They're simply based on the observation that under certain constraints, when executing search, one can do efficient memoization. If you throw away the "magic" of Viterbi and treat it as jsut another search algorithm, you see that there's nothing special there.

I have a hard time convincing people of 2. I'm not quite sure why. I almost liken it to trying to convince a classically trained logician the ways of constructive logic are right (being one of the former, I'm not yet convinced). The problem is that we're so used to seeing VS as this very special array-filling operation that we forget what's really going on. We could just as easily do search and store stuff in a hash table. It wouldn't be quite as efficient, but complexity wise (assuming O(1) access to the table), it would be the same.

The "magic" of Viterbi is that it efficiently integrates all information from the different sources assuming that the conditional independences hold and assuming that all conditional probabilities are correctly estimated. But we know this is not the case.

That said, I think there is something to be said for later decisions being able to influence earlier ones. But I don't take this as given. And I don't think it's always the case. This is a big open question for me. By using a more complex search algorithm, you're forcing more decisions to be made but are (we hope) making these decisions easier. This is a trade-off. One angle is not a priori better than the other.

Snowbird Accepted Papers Up

The list of accepted papers for the Snowbird Learning Workshop is up. I'm interested to see:

• Training CRFs with SMD (Vishwanathan, Shraudolph, Schmidt + Murphy)
  
• Sub-gradient method structured learning (Bagnell, Ratliff + Zinkevich)
• AdaBoost is MaxEnt over the error distribution (Haffner)
• Structural correspondences for transfer learning (Blitzer, Crammer, McDonald + Pereira)
• Rule-extraction from SVMs (Braun + Buhmann)
• Prior beliefs in SSL (Luxburg + Ben-David)
• Model compression (Caruana, Bucila + Niculescu-Mizil)

Is X useful for Y?

This post has two parts, both addressing the issue of showing that one task (X) is useful for another task (Y); eg., syntax is useful for MT, or WSD is useful for IR, or ....

The first question is: on whom is the onus of making such an argument. (I'm presupposing that it makes sense to make such an argument.) There are three options: (1) a person who does X; (2) a person who does Y; a third party. Arguments in favor of 1: if I work on a task, I am likely to want to justify its importance. For 2: I know the most about Y, so if X is useful, I can probably get it to work; also, other (2)s are more likely to buy my results. For 3: ???.

One could argue (3) to be (more) unbiased, but I'll make an idealized assumption that (1) and (2) care about furthering science, not some personal research program. Given that, I think the best case scenario is to have a joint authored paper between a (2) and a (1); that failing, I'd probably prefer a paper by a (2). I'd prefer it not from a potential bias perspective, but because a (2) is more likely to produce a Y-system that's state-of-the-art, so showing that X improves on this is going to be more convincing. Of course if a (1) can do that, that's fine too.

The second issue that I see is that in a lot of cases it's not cut and dry. Take for example a recent paper that showed that syntax is useful for EDT. I believe this paper is probably right, given the maturity of the system into which syntax was added. However, take my EDT system. I worked on this for about 15 months not using syntax. I used all sorts of crazy features. If I add syntax (which I've done), it improves things a little. Not a lot. And only for coref, not for mention tagging. Why? Likely, I've engineered around having syntax. If I had added syntax at the beginning, maybe I could have done away with many of the other features I have. We see the same thing in IR: if some complex NLP technique seems to improve IR systems but is expensive to run, then often people will keep tearing it apart until they find some tiny little feature that's doing all the important work. If so, can we still say that the original task helped?

I think, given this, there is a better way to measure the usefulness of X to Y other than: X improved Y's performance. Consider someone setting out to build an EDT system. They want to know whether they should include syntax or not. The real question is: assuming I get comparable performance, is it easier to include syntax or to engineer around it. I don't know how to measure this automatically (lines of code is perhaps a reasonable surrogate, assuming the same coder writes both), but it seems like such a measure would be much more useful and telling than whether or not performance on an arbitrary system goes up.

HLT-NAACL Program Up

The program for HLT-NAACL 2006 has been posted (I didn't submit anything). I'm partcularly looking forward to:

• A fast finite-state relaxation method (Tromble + Eisner)
• Name matching in English and Arabic (Freeman, Condon + Ackerman)
• Do we need phrases? (Quirk + Menezes)
• Using syntax for false entailment (Snow, Vanderwende + Menezes)
• Grammatical machine translation (Riezler + Maxwell)
• SRL, Wornet and Wikipedia for Coreference (Ponzetto + Strube)

I'm sure others will be good too. Anyone see anything else especially intruiging?

Evaluation Criterea: Correlation versus Generalization

When developing a "third level" loss function (i.e., an automatic metric), one often shows that the ranking or the scores of the automatic function correlates well with the ranking or scores of the human-level function.

I'm not sure this is the best thing to do. The problem is that what correlation tell us is just that: on the data sample we have, our automatic evaluation function (AE) correlates well with the human evaluation function (HE). But we don't actually care (directly) about the correlation on past data. We are about the ability to make future predictions of quality. Namely, we often want to know:

If I improve my system by 1 point AE, will this improve my HE score?

This is a generalization question, not a correlation question. But we know how to analyze generalization questions: Machine learning theorists do it all the time!

So, what do we know: if we want AE to predict HE well in the generalization sense, then it is (with high probability) sufficient that AE predicts HE well on our observed (training) data, and that AE is not "too complex." Usually this latter holds. AE is often chosen to be as simple as possible, otherwise people probably won't buy it. Usually it's chosen from a small finite set, which means we can do really simple PAC-style analyses. So this should be enough, right: we have good prediction of the training data (the correlation) and a small hypothesis class, so we'll get good generalization. Thus, correlation is enough.

Well, not quite.

Correlation+small hypothesis class is enough only when the "training data" is i.i.d. And our problem assumptions kill both of the "i"s. First, our data is not independent. In summarization (and to a perhaps slightly lesser extent in MT), the systems are very very similar to eachother. In fact, when people submit multiple runs, they are hugely similar. Second, our data is not identically distributed to the test data. The whole point of this exercise was to answer the question: if I improve my AE will by HE improve? But, at least if I have the top system, if I improve my AE too much, my system is no longer from the same distribution of systems that generated the training data. So the data is hardly i.i.d. and easy generalization bounds cannot be had.

So what can we do about this? Well, recognizing it is a start. More practically, it might be worth subsampling from systems when deriving correlation results. The systems should be chosen to be (a) as diverse as possible and (b) as high performance as possible. The diversity helps with independence. The high performance means that we're not geting supurb correlation on crummy systems and no correlation on the great systems, leading to poor generalization as systems get better. This doesn't fix the problem, but it might help. And, of course, whenever possible we should actually run HE.

Structured Prediction 3: What's to Come

Different researchers have different priorities, and not all those listed here are things I personally plan to work on. There are many open questions about structured prediction that I'd like an answer to. Hopefully we'll make some headway at the atomic learning workshop, and I'll of course post after that.

1. Move to more complex, "intractable" structures.
2. More with less: improving with only weak feedback.
3. Learning structure: the analogue of learning graphical models.
4. Learning from heterogenous data.
5. Measuring sample complexity.
   
6. Trading off expressivity with tractability.
7. Integrated prediction and data mining.
8. Computational complexity versus sample complexity.

My short term goal is [1] and [6] (and I've worked a bit on [4], but not for SP). Andrew McCallum seems to be working hard on [1] (though using different machinery) and [7]. I think Ben Taskar has some new work on [1] and is probably closer to [5] than any of us. Thorsten Joachims has done interesting work in [1] and [2] (the latter not for SP though), but I think (hope) he might bring some of that across. I don't really know who (if anyone!) is working on the other topics.

The question that drives me is: to what extent can we let the NLPer forget about the fact that there's machine learning going on in the background. I think that, as of now, at least from my perspective, the answer is that the NLPer must be able to structure a search space for his problem, and devise a way for turning the "true output" into an "optimal policy" by breaking it down into regions. The rest is purely trivial crank turning (no math required). The answers to the questions above will help in this endeavor. A very basic question, hinted on before, is: when do we even need to consider structure? If we don't, life is much easier for the NLPer. But we need to be able to say when we do and when we don't need structure. And when we do, we want it to be as painless as possible.

Tutorial: Bayesian Techniques for NLP

I'm giving a tutorial on Bayesian methods for NLP at HLT-NAACL 2006. I gave a similar tutorial about a year ago here at ISI. This gave me a pretty good idea of what I want to keep in and what I want to cut out. The topics I intend to cover are, roughly:

1. Bayesian paradigm: priors, posteriors, normalization, etc.
2. Graphical models, expectation maximization, non-bayesian inference techniques
3. Common statistical distributions: uniform, binomial/multinomial, beta/dirichlet
4. Simple inference: integration, summaring, monte carlo
5. Advanced inference: MCMC, Laplace, Variational
6. Survey of popular models: LDA, Topics and Syntax, Words and Pictures
7. Pointers to literature

All of this is, of course, cast in the context of NLP problems: all discrete distributions, language applications, etc., that hopefully both NLP and IR people will find interesting (maybe even some speech people, too).

Does anyone have anything they'd really like to hear that's not on the list? Or anything that's on the list that they don't care about? Keep in mind several constraints: 3 hours (minus coffee time), generally accessible, focused on NLP applications, and something I know something about. (For instance, I covered expectation propagation in the tutorial last year, but decided to cut it for this to give more time to other issues.) Note that I am also preparing a written tutorial that covers roughly the same material.

Structured Prediction 2.5: Features

I decided to add an additional post on structured prediction before the final one. This is also highly related to the post on joint inference.

One can claim that when doing structured prediction, the features X never have longer range than the loss function, where X is either "need" or "should." To this day I struggle to understand this issue: I don't believe it is as simple as one would like.

Consider our old favorite: sequence labeling under Hamming (per label) loss. The arguement essentially goes: we don't care (i.e., our loss function doesn't care) about how well our labels fit together. All it cares about is getting each right individually. By essentially the same argument as the joint inference post, one can then see that one should train a single classifier that does not use any "Markov-style" features.

On the other hand, I know that I have always seen Markov-style features to help, and I believe that most people who work on SP would agree.

Just as in the joint inference case, I think that if you want to be guaranteed the same information to train a classifier on, you need to move to a cross-product feature space. Unlike John, I do fear this. I fear this for several reasons. First, we already have millions of features. Going to 10^12 features is just not practical (blah blah kernels blah blah). This can also lead to severe generalization issues, and I don't think the state of the art in machine learning is capable of dealing with this. It's trikcy, though, because I largely believe the joint inference argument, and largely don't believe this argument. Yet they are essentially the same.

But I think there might be a more fundamental issue here, beyond cross-product feature spaces, generalization bounds and so on. This is the issue of: if we know a problem has structure, even if the loss function (even the true one) doesn't reflect this, should we make use of this structure. The answer to "Why?" is that it might make it easier on our models to learn. The answer to "Why not?" is that by doing so we require more "human in the loop" than otherwise.

The Art of Loss Functions

There are roughly four types of loss functions that are used in NLP research.

1. The real loss function given to us by the world. Typically involves notions of money saved, time saved, lives saved, hopes of tenure saved, etc. We rarely have any access to this function.


2. The human-evaluation function. Typical examples are fluency/adequecy judgments, relevance assessments, etc. We can perform these evaluations, but they are slow and costly. They require humans in the loop.


3. Automatic correlation-driving functions. Typical examples are Bleu, Rouge, word error rate, mean-average-precision. These require humans at the front of the loop, but after that are cheap and quick. Typically some effort has been put into showing correlation between these and something higher up.


4. Automatic intuition-driven functions. Typical examples are accuracy (for anything), f-score (for parsing, chunking and named-entity recognition), alignment error rate (for word alignment) and perplexity (for language modeling). These also require humans at the front of the loop, but differ from (3) in that they are not actually compared with higher-up tasks.

Note that the difference between (3) and (4) changes over time: there are many (4)s that could easily become (3)s given a few rounds of experimentation. (I apologize if I called something a (4) that should be a (3).)

It is important to always keep in mind that our goal is to improve (1). The standard line is: I can't compute (1) so I approximate it with (2). I can't optimize (2) so I approximate it with (3). (Or, I don't know how to define (2) so I approximate it with (4).)

I strongly feel that the higher up on this list one is, the harder it is to actually define the evaluation metric. It is very easy to define things at the (4) level because there are essentially no requirements on such a loss function other than (A) hard to game and (B) intuitively reasonable. It is a bit harder to define things at the (3) level because an additional critereon is added: (C) must be able to convince people that this new loss function approximates an established (1) or (2). Defining something at the (2) level is shockingly difficult and (1) is virtually impossible.

There are two questions that are crutial to progress. The first is: what is the minimum acceptable evaluation. We cannot reasonably require (1) in all cases. In many cases, I think it absolutely reasonable to require (2); eg. journal papers for which a working definition of (2) is known. Conference papers can usually get by with (3) or (4). I would never accept (4) when a (3) is known. But when not (consider named entity recognition), it's all we have.

It's unclear if this is a good breakdown or not. I could argue never to accept (4): that you must show your results improve something humans care about, at least approximately. But this seems limiting. First, it means that if we want to solve a subproblem, we have to formally show that solving it will be useful before we actually solve it. This is a good thing to do a but of internally, but to do a sophisticated analysis to the point of publishable results to move something from (4) to (3) is a lot of effort for (often) little gain. Especially in the context of a larger research agenda.

I could also argue that for many results, (4) is always sufficient. The argument here is that, from a machine learning perspective, if I can optimize (4), I can optimize anything else you give me. While I've made this argument personally, it's just not true. A more complex loss function might be much harder to optimize (consider optimizing Bleu-1 without brevity penalty versus full Bleu-4). Moreover, it may turn out that whatever biases my model has are good for one (4) and not for another. This is an okay (but not great) argument in an ML conference, but I wouldn't buy it in NLP.

So how do other people rank these things? How much pressure is there to bring a (4) to a (3)? And how often should we do (2)?

Joint Inference

Joint inference is becoming really popular these days. There's even a workshop coming up on the topic that you should submit a paper to! (That is, unless your paper is more related to the computationally hard NLP workshop I'm running with Ryan McDonald and Fernando Pereira).

The problem with joint inference is that while it seems like a great idea at the outset -- getting rid of pipelining, etc. -- in theory it's not always the best choice. I have a squib on the topic, titled Joint Inference is not Always Optimal and I welcome any and all comments/criticisms/etc.

Predictive Models

There are at least two reasonable goals for NLP research: (1) produce predictive systems that mimic humans; (2) produce explanatory models. (2) gets more into CL and CogSci and I may discuss it at a later date. This post is about (1), at least the machine learning approach to (1).

Our goal is to mimic a human on some task. This means we will, at the end of the day, want to measure our performance against human performance. This measurement is our loss function, and is, in my mind, the only thing that really matters. Coming up with a good loss function is really really hard and I will certainly discuss this issue in another post. But suppose we can come up with one: l(t,h) = how much it hurts to produce a hypothesis h when the true answer was t.

The subsequent question is: given some collected data, how can I minimize l. The dominant approach seems to be: approximate l by some well-known loss (binary loss, squared error, absolute loss, etc.) and then use one of the many good classifiers/regressors to solve our original problem.

This step irks me greatly. Not because this approximation is always bad, but because it is never (rarely) stated. Many papers say something like "Our task in XYZ is to minimize misclassification error of problems created by ABC." This is rarely actually true. I would be much happier with the following explanation: "Our task in XYZ is to minimize TUV loss, but we don't know how to do that, so we'll instead minimize misclassification error." This issue manifests itself commonly in another way: putting the cart before the horse. We often gather a data set, label it, solve the labeling problem (eg., by multiclass classification) and then go back and define the problem in such a way that this is an appropriate solution. This is harder to detect, but equally disingenuous.

So let's say we've done things right: we've defined our loss function and we've gotten some labeled data. Now we have to minimize our loss on this data. If we can do this directly, great. If not, we can say so and that we'll approximate it by some other loss l'.

Now we can start looking at features. We have an l' that we can minimize and we want to come up with features that are useful for this minimization. In particular, if ours is a structured problem, and l' is invariant to some change in structure, we needn't reflect this aspect of the structure in our feature functions function (the prototypical example here being Markov features in sequence labeling for Hamming [per-label] loss, though this issue itself could take a whole other post). We should set aside part of the training data for manual inspection to do feature engineering.

Experimentation is the last real step. We've split off a training set, development set and test set (*). We train a model on the training set, evaluate it on the development set. We look at the dev predictions and see what went wrong. We reengineer some features to fix these problems and repeat. Only at the end do we run on the test set and report our results in a paper.

(*) I'm not a fan of cross-validation in such a cyclic process. The features will be engineered based on the training and development data sets, and to then fold all this back into the bag and do cross-validation will give us unrealistically good results.

And as a very final step, in the case that our optimized l' is not the same as l, I would like to see some results that show that they at least correlate reasonably well. And easy way to do this is to run several versions of the model and to report both l and l' scores and let us see that improving l' does indeed improve l.

Domain Adaptation

We NLPers face this problem all the time: we have training data from one domain/genre but really want to work in another. Eg., the treebank is WSJ text but we care about email or web pages or whatever. We'd like to be able to intelligently use our annotated WSJ text to get a good statistical model for a different domain.

I've been working on this problem for a while now and have a partial solution. I'm most interested in the case that we have lots of annotated "out of domain" (OOD) data and a little annotated "in domain" (ID) data. Domain Adaptation for Statistical Classifiers is a paper that's been accepted to JAIR that presents one way to model this problem. The key idea is to model the OOD/ID data distributions as mixtures. There are three mixture components: a "truly ID" distribution, a "truly OOD" distribution and a "general" distribution. We say the OOD data comes from a mixture of "truly OOD" and "general," while the ID data comes from a mixture of "truly ID" and "general." The learning task is to tear apart our data sets to figure out what "general" (and hence relevant to the ID task) information there is in the OOD data.

The framework, when applied to maximum entropy models, gives relatively simple update equations for model parameters. The derivations take a bit of thought, but are not insane. The approach is a partial solution because it's limited to maximum entropy models. I think the problem should be amenable to a more learning theoretic analysis, but haven't had time to make much headway here.

I'm a bit surprised this problem hasn't gotten more attention in the NLP community (a similar problem -- speaker adaptation -- exists in the speech community). Or perhaps I've missed it in NLP. It seems like we, as NLPers, should really care about this issue.

Most Influential NLP Papers

I conducted a mini survey recently, asking people I knew what they thought were the most influential papers in NLP from the past two decades. Here are the wholly unscientific results, sorted from most votes and subsorted by author. Note that I only got responses from 7 people. I've not listed papers that got only one vote and have not included my personal votes.

(7 votes): Brown et al., 1993; The Mathematics of Statistical Machine Translation
(5 votes): Collins, 1997; Three Generative, Lexicalised Models for Statistical Parsing
(4 votes): Marcus, 1993 Building a large annotated corpus of English: the Penn Treebank
(3 votes): Berger et al., 1996; A maximum entropy approach to natural language processing
(2 votes): Bikel et al., 1997; An Algorithm that Learns What's in a Name
(2 votes): Collins, 2002; Discriminative Training Methods for Hidden Markov Models: Theory and Experiments with Perceptron Algorithms
(2 votes): Lafferty et al., 2001; Conditional Random Fields: Probabilistic Models for Segmenting and Labeling Sequence Data
(2 votes): Och, 2003; Minimum Error Rate Training for Statistical Machine Translation
(2 votes): Papineni et al., 2001; Bleu: a method for automatic evaluation of machine translation
(2 votes): Ratnaparkhi, 1999; Learning to Parse Natural Language with Maximum Entropy Models
(2 votes): Yarowsky, 1995; Unsupervised Word Sense Disambiguation Rivaling Supervised Methods

This seems to be dominated by parsing and techology/machine learning papers, with a smattering of MT thrown in for good measure. I feel that the former represent a sort of "lowest common demoninator." There were several singleton votes for various papers in summarization, language modeling, IR, and other fields, but, with the exception of the MT papers, getting >1 vote meant that you had to be useful to more than just your one community. It's also a bit surprising that Collins' parser is so high, but no other parsers got any votes (Charniak, Lin, etc.).

Feel free to say what you think is missing!

Structured Prediction 2: My Perspective

In Structured Prediction 1: What's out there?, I discussed current SP technology: Markov fields, CRFs, M3Ns and SVMISOs. Here I'll discuss my work briefly. I'll come back to SP once more to discuss what seems to be on the horizon.

With so many options, why bother with a new one? There are problems that are not solved by the standard approaches. The biggest problem is the "argmax assumption," which states that you can solve the following problem:

arg max_{y in Y} f(x,y; w) = arg max_{y in Y} w*Phi(x,y)

Where the equality is under the standard linear predictor assumption. This maximization requires that, for an input x, we are able to compute the highest scoring possible output (efficiently).

The problem is that for many (most?) NLP problems, without making completely unreasonable assumptions, this maximization is intractable. The standard assumptions that make this operation polynomial time are the Markov assumption for sequences and the context-free assumption for trees. But we know that both of these assumptions are invalid, and a few papers have tried to deal with this by using sampling, reranking or approximate inference techniques.

On the other hand, if you look at what people in NLP actually do to solve problems, they use approximate search (MT is a good example). In this way, the search space can be tuned to precisely capture the functional (feature) dependencies needed.

My perspective is that if we're going to use search anyway, we should take this into account while learning. There is no point to learning a model that ranks the best output highest if we cannot actually find this output. And once we start using approximate search, any performance guarantees related to learning pretty much go out the window.

The really cool thing is that a completely different brand of machine learning people have considered learning in the context of search, but they call it reinforcement learning. The key difference between SP and RL, as I see it, is that in RL you can affect the world whereas in SP you cannot. In the standard "action/state/observation" terminology, in SP you only get one observation at the very beginning (the input x), while in RL the observations keep coming in as you take more actions. This seems to be the fundamental difference between the two problems.

So, by treating SP in a search framework, what we basically want is a function that takes our input x, a partial output represented by a state in our search space s, and predicts the best action to take: the best thing to add onto the partial output. For instance, in sequence labeling with left-to-right decoding, we might predict the label of the next word. In MT, we might predict a French phrase the translate and its English translation and append this to a translation prefix. The action set is potentially large, but not impossibly so (if it were, the problem would be intractable anyway).

The great thing is that this enables us to formally cast structured prediction as a cost-sensitive multiclass classification problem. Lots of algorithms have been developed for the multiclass problem, and we can seek to apply these to the SP problem through this reduction. This gives us simple, efficient algorithms with good practical performance and strong theoretical guarantees. The key requirement that makes all this work (essentially my version of the arg max assumption) is that for a given input x, true output y and state s in the search space, we can compute the action a that is optimal to execute from s. This is the "optimal policy assumption." (We can actually weaken this assumption to require only a bound on the optimal policy, which is necessary for optimizing things like BLEU or ROUGE, at least under interesting models.) It is provably a strictly weaker assumption than the assumptions made by CRFs and M3Ns, essentially because it doesn't care about the feature space, which means we can have whatever the heck features we want (a good thing for NLP).

The MT Blues: Would a program get its facts right?

I just came across an article on Slate entitled The Translator's Blues: Will I get replaced by a computer program?, written by Jesse Browner, a human translator. I've no idea how wide-read Slate is, and I think Browner is correct that his job is not (yet) in jeopardy, there are several common misconceptions in the article that really shouldn't be there.

First, the results of his example sentence are atrocious. I see no reason why even the rule-based systems should get this wrong (though I suspect his poor results had to do largely with the difficulty of inputting accented characters). Language Weaver stood out, which is good, because it's a good system. In fact, in all the news texts he tried, it is reported to fare well.

And he's right that the technology has limits: it could not translate the first sentence of Don Quixote well. This is the domain adaptation problem: Language Weaver's system was trained on news data and (surprise surprise) it performs well on news and not on fiction. I think the important point is that the problem is domain. IMO, it has nothing to do with context, which is what Browner attributes the problem to. The con/pen example is something that I believe a decent statistical MT system should and would get right; if not now, in a few years once language models are better. It's unfortunate that Browner doesn't say that Language Weaver is (largely) a statistical systems, because he seems to say that they suck, yet LW was by far the best system he tried.

My final comment is in reference to the attribution to Mike Collins, who clearly knows much more about this field than many. Most likely Mike was quoted out of context, but Language Weaver's system -- and, in fact, most good research systems out there -- are based on machine learning. That's what "statistical" means.

(Incidentally, for those less literary minded, the first sentence of Don Quixote should be translated something like "In a village of La Mancha, the name of which I have no desire to call to mind, there lived not long since one of those gentlemen that keep a lance in the lance-rack, an old buckler, a lean hack, and a greyhound for coursing." I'm not convinced that a professional translator who worked for the UN would find this easy to translate either.)

NLP as Glorified Memorization

The view of NLP as essentially a hunt-and-return technology has been gathering momentum since the burgeoning of the web. Example-based MT takes this view to machine translation, and phrase-based statisitcal MT is essentially EBMT done with statistics. In question answering (factoid style), the situation is even more dramatic. Deepak's thesis was essentially devoted to the idea that the answer to any question can be found in huge corpora by relatively simple pattern-matching. To a somewhat lesser degree, information extraction technology is something like smoothed (or backed-off) memorization, and performance is largely driving by one's ability to obtain gazeteers relevant to one's task.

Pushing such memorization technology further will doubtless lead to continued success, and there are many open research questions here. I would love others to answer these questions, but I have little interest in answering them myself. Fortunately, I think there are many interesting real-world problems for which simple memorization techniques will not work, and deeper "analysis" or "understanding" is required.

Any QA/summarization task that focuses on something other than "general world knowledge" fits into this category. I might want to ask questions to my email client about past emails I've recieved. The answer will likely exist only once, and likely not in the form I ask the question. I might want to ask questions about scientific research, either from PubMed or REXA. I might want to ask about the issues involved in the election of the Canadian PM (something I know nothing about) or the confirmation hearings of Samuel Alito (something I know comparatively more about). And I would want the answers tailored to me. If I owned a large corporation or were running a campaign, I would want to know what my supporters and detractors were saying about me, and who was listening to whom.

I could be proven wrong: maybe memorization techniques can solve some/all of these problems, but I doubt it. What other problems are people interested in that may not be solvable with memorization?

Long Distance Collaboration

For those who have engaged in such an affair, I'm curious how you make it work well. I've been working with John Langford recently, drawing out and exploiting connections between structured prediction and reinforcement learning. I'm visiting family in Chicago now and will be going to TTI tomorrow to visit. Up until this visit, we've talked mostly over email, less over phone and even less in person (some at ICML and NIPS 2005). But the rate of information transfer in such collaboration is significantly less than if John had an office down the hall from me. How do people make this work?

1. Site visits. This is/was the defacto standard in business for ages, before the internet came. People also tended to collaborate less and in business there is perhaps less of a push for collaboration rather than subcontracting. While undoubtedly the best method for interacting, there is significant overhead in terms of cost, travel time, etc., especially in different continents.
2. Telephone. Another good business standard; unfortunately, I'm really a white-board kind of guy, and it's really hard to draw on someone else's white board. Talking about math and referencing papers is also difficult over the phone. Large time differences can also be a nuisance (I recall talking to Yee Whye at about midnight my time because of the time difference to Singapore).
   
3. E-mail. This seems to be what is used most: it is cheap and doesn't suffer from the time difference, though replies are delayed. It enables you to think more about a topic before replying, but cuts down on often-constructive back-and-forth discussion (since that would take too long). The medium is also limited: typing math into email is ugly for anything complex, and you still can't draw on someone else's white board. Twice in my life I've attached .eps figures, but this is highly ineffective.
   

So, what do other people do? Is there any hope? It seems that email could theoretically be retrofitted to fix a lot of the problems I have with it (multiple media, drawing, math, etc.), but does such technology exist currently?

The Mad Paper Rush

The HLT/NAACL deadline passed last month and the ACL deadline is next month. The cluster here seems more swamped than usual, people are rushing to get experiments done and papers written. It seems that most research gets done two months prior to the due dates and papers are rarely, if ever, submitted early. (Actually, I saw a statistic from ICML that most early-submitted papers actually got rejected in the end!) As someone who is trying to organize a ski trip to Mammoth two weeks before the ACL deadline and having difficulty getting people to come, I wonder why there's always this last minute rush. The ACL deadline was published at least four months ago, and even if not, it's actually later this year than usual.

The only explanation that makes sense to me is that the rush is to run a handful of well-controlled experiments based on continuous tweaking of a system. The further you can delay running these experiments, the more you can tweak. Importantly, assuming you're a good researcher, the experiments are not to convince yourself that your approach is viable. The experiments are to convince your potential reviewers that your approach is viable.

Based on this, there seem to be two ways to cut down on this rush (assuming people don't like it). First is to reduce the amount of tweaking done. Second is to reduce the number of well-controlled experiments run. Unfortunately, both of these will probably result in lower chances of your paper being accepted (confirming the above-cited ICML statistic). But this is bad. Tweaking will improve your scores (hopefully), but will rarely be mentioned in the paper, leading to irreproducible results. Running too many experiments can cloud the point of your paper and significantly cut down on your time to work on real things.

Despite this, people continue to tweak and run too many experiments (myself included). This seems to be because the cost of failure is too high: if your paper is rejected, you basically have to wait another year to resubmit, so you want to cover all bases. Two solutions come to mind. First, we could spread our conferences further apart, meaning that you have only to wait 6 months. Second, we could try to ensure that reviewers know that with a limit of 8 pages, one cannot run all possible experiments, and that they can suggest alternative contrastive experiments to be run, but if the experiments back up the main point(s) of the paper, this should be sufficient. I don't think the "review/response" approach will fix this because running a new experiment is not what author responses are for, and this is just delaying the problem, rather than fixing it (though I do advocate the response phase).