Machine Learning (Theory)


The Benefits of Double-Blind Review

This post is a (near) transcript of a talk that I gave at the ICML 2013 Workshop on Peer Review and Publishing Models. Although there’s a PDF available on my website, I’ve chosen to post a slightly modified version here as well in order to better facilitate discussion.

Disclaimers and Context

I want to start with a couple of disclaimers and some context.

First, I want to point out that although I’ve read a lot about double-blind review, this isn’t my research area and the research discussed in this post is not my own. As a result, I probably can’t answer super detailed questions about these studies.

I also want to note that I’m not opposed to open peer review — I was a free and open source software developer for over ten years and I care a great deal about openness and transparency. Rather, my motivation in writing this post is simply to create awareness of and to initiate discussion about the benefits of double-blind review.

Lastly, and most importantly, I think it’s essential to acknowledge that there’s a lot of research on double-blind review out there. Not all of this research is in agreement, in part because it’s hard to control for all the variables involved and in part because most studies involve a single journal or discipline. And, because these studies arise from different disciplines, they can be difficult to
track down — to my knowledge at least, there’s no “Journal of Double-Blind Review Research.” These factors make for a hard landscape to navigate. My goal here is therefore to draw your attention to some of the key benefits of double-blind review so that we don’t lose sight of them when considering alternative reviewing models.

How Blind Is It?

The primary motivation behind double-blind peer review — in which the identities of a paper’s authors and reviewers are concealed from each other — is to eliminate bias in the reviewing process by preventing factors other than scientific quality from influencing the perceived merit of the work under review. At this point in time, double-blind review is the de facto standard for machine learning conferences.

Before I discuss the benefits of double-blind review, however, I’d like to address one of its most commonly heard criticisms: “But it’s possible to infer author identity from content!” — i.e., that double-blind review isn’t really blind, so therefore there’s no point in implementing it. It turns out that there’s some truth to this statement, but there’s also a lot of untruth too. There are several studies that directly test this assertion by asking reviewers whether authors or institutions are identifiable and, if so, to record their identities and describe the clues that led to their identification.

The results are pretty interesting: when asked to guess the identities of authors or institutions, reviewers are correct only 25–42% of the time [1]. The most common identification clues are self-referencing and authors’ initials or institution identities in the manuscript, followed by reviewers’ personal knowledge [2, 3]. Furthermore, higher identification percentages correspond to journals in which papers are required to explicitly state the source of the data being studied [2]. This indicates that journals, not just authors, bear some responsibility for the degree of identification clues present and can therefore influence the extent to which review is truly double-blind.

Is It Necessary?

Another commonly heard criticism of double-blind review is “But I’m not biased!” — i.e., that double-blind review isn’t needed because factors other than scientific quality do not affect reviewers’ opinions anyway. It’s this statement that I’ll mostly be focusing on here. There are many studies that address this assertion by testing the extent to which peer review can be biased against new ideas, women, junior researchers, and researchers from less prestigious universities or countries other than the US. In the remainder of this post, I’m therefore going give a brief overview of these studies’ findings. But before I do that, I want to talk a bit more about bias.

Implicit Bias

I think it’s important to talk about bias because I want to make it very clear that the kind of bias I’m talking about is NOT necessarily ill-intentioned, explicit, or even conscious. To quote the AAUW’s report [4] on the under-representation of women in science, “Even individuals who consciously refute gender and science stereotypes can still hold that belief at an unconscious level. These unconscious beliefs or implicit biases may be more powerful than explicitly held beliefs and values simply because we are not aware of them.” Chapters 8 and 9 of this report provide a really great overview of recent research on implicit bias and negative stereotypes in the workplace. I highly recommend reading them — and the rest of the report for that matter — but for the purpose of this post, it’s sufficient to remember that “Less-conscious beliefs underlying negative stereotypes continue to influence assumptions about people and behavior. [Even] good people end up unintentionally making decisions that violate [...] their own sense of what’s correct [and] what’s good.”

Prestige and Familiarity

Perhaps the most well studied form of bias is the “Matthew effect,” originally introduced by Robert Merton in 1968 [5]. This term refers to the “rich-get-richer” phenomenon whereby well known, eminent researchers get more credit for their contributions than unknown researchers. Since 1968, there’s been a considerable amount of follow-on research investigating the extent to which the Matthew effect exists in science. In the context of peer review, reviewers may be more likely to recommend acceptance of incomplete or inferior papers if they are authored by more prestigious researchers.

Country of Origin

It’s also important to consider country of origin and international bias. There’s research [6] showing that reviewers from within the United States and reviewers from outside the United States evaluate US papers more favorably, with US reviewers showing a stronger preference for US papers than non-US reviewers. In contrast, US and non-US reviewers behaved near identically for non-US papers.


One of the most widely discussed pieces of recent work on double-blind review and gender is that of Budden et al. [1], whose research demonstrated that following the introduction of double-blind review by the journal Behavioral Ecology, there was a significant increase in papers authored by women. This pattern was not observed in a similar journal that instead reveals author information to reviewers. Although there’s been some controversy surrounding this work [7], mostly questioning whether the observed increase was indeed to do with the policy change or a more widely observed phenomenon, the original authors reanalyzed their data and again found that double-blind review favors increased representation of female authors [8].


Race has also been demonstrated to influence reviewers’ recommendations, albeit in the context of grant funding rather than publications. Even after controlling for factors such as educational background, country of origin, training, previous research awards, publication record, and employer characteristics, African-American applicants for National Institutes of Health R01 grants are 10% less likely than white applicants to be awarded research funding [9].

Stereotype Threat

I also want to talk briefly about stereotype threat. Stereotype threat is a phenomenon in which performance in academic contexts can be harmed by the awareness that one’s behavior might be viewed through the lens of a negative stereotype about one’s social group [10]. For example, studies have demonstrated that African-American students enrolled in college and female students enrolled in math and science courses score much lower on tests when they are reminded beforehand of their race or gender [10, 11]. In the case of female science students, simply having a larger ratio of men to women present in the testing situation can lower women’s test scores [4]. Several factors may contribute to this decreased performance, including the anxiety, reduced attention, and self-consciousness associated with worrying about whether or not one is confirming the stereotype. One idea that that hasn’t yet been explored in the context of peer review, but might be worth investigating, is whether requiring authors to reveal their identities during peer review induces a stereotype threat scenario.

Reviewers’ Identities

Lastly, I want to mention the identification of reviewers. Although there’s much less research on this side of the equation, it’s definitely worth considering the effects of revealing reviewer identities as well — especially for more junior reviewers. To quote Mainguy et al.’s article [12] in PLoS Biology, “Reviewers, and especially newcomers, may feel pressured into accepting a mediocre paper from a more established lab in fear of future reprisals.”


I want to conclude by reminding you that my goal in writing this post was to create awareness about the benefits of double-blind review. There’s a great deal of research on double-blind review and although it can be a hard landscape to navigate — in part because there are many factors involved, not all of which can be trivially controlled in experimental conditions — there are studies out there that demonstrate concrete benefits of double-blind review. Perhaps more importantly though, double-blind review promotes the PERCEPTION of fairness. To again quote Mainguy et al., “[Double-blind review] bears symbolic power that will go a long way to quell fears and frustrations, thereby generating a better perception of fairness and equality in global scientific funding and publishing.”


[1] Budden, Tregenza, Aarssen, Koricheva, Leimu, Lortie. “Double-blind review favours increased representation of female authors.” 2008.

[2] Yankauer. “How blind is blind review?” 1991.

[3] Katz, Proto, Olmsted. “Incidence and nature of unblinding by authors: our experience at two radiology journals with double-blinded peer review policies.” 2002.

[4] Hill, Corbett, St, Rose. “Why so few? Women in science, technology, engineering, and mathematics.” 2010.

[5] Merton. “The Matthew effect in science.” 1968.

[6] Link. “US and non-US submissions: an analysis of reviewer bias.” 1998.

[7] Webb, O’Hara, Freckleton. “Does double-blind review benefit female authors?” 2008.

[8] Budden, Lortie, Tregenza, Aarssen, Koricheva, Leimu. “Response to Webb et al.: Double-blind review: accept with minor revisions.” 2008.

[9] Ginther, Schaffer, Schnell, Masimore, Liu, Haak, Kington. “Race, ethnicity, and NIH research awards.” 2011.

[10] Steele, Aronson. “Stereotype threat and the intellectual test performance of African Americans.” 1995.

[11] Dar-Nimrod, Heine. “Exposure to scientific theories affects women’s math performance.” 2006,

[12] Mainguy, Motamedi, Mietchen. “Peer review—the newcomers’ perspective.” 2005.


Representative Reviewing

Tags: Conferences,Reviewing ,Workshop jl@ 10:09 am

When thinking about how best to review papers, it seems helpful to have some conception of what good reviewing is. As far as I can tell, this is almost always only discussed in the specific context of a paper (i.e. your rejected paper), or at most an area (i.e. what a “good paper” looks like for that area) rather than general principles. Neither individual papers or areas are sufficiently general for a large conference—every paper differs in the details, and what if you want to build a new area and/or cross areas?

An unavoidable reason for reviewing is that the community of research is too large. In particular, it is not possible for a researcher to read every paper which someone thinks might be of interest. This reason for reviewing exists independent of constraints on rooms or scheduling formats of individual conferences. Indeed, history suggests that physical constraints are relatively meaningless over the long term — growing conferences simply use more rooms and/or change formats to accommodate the growth.

This suggests that a generic test for paper acceptance should be “Are there a significant number of people who will be interested?” This question could theoretically be answered by sending the paper to every person who might be interested and simply asking them. In practice, this would be an intractable use of people’s time: We must query far fewer people and achieve an approximate answer to this question. Our goal then should be minimizing the approximation error for some fixed amount of reviewing work.

Viewed from this perspective, the first way that things can go wrong is by misassignment of reviewers to papers, for which there are two
easy failure modes available.

  1. When reviewer/paper assignment is automated based on an affinity graph, the affinity graph may be low quality or the constraint on the maximum number of papers per reviewer can easily leave some papers with low affinity to all reviewers orphaned.
  2. When reviewer/paper assignments are done by one person, that person may choose reviewers who are all like-minded, simply because
    this is the crowd that they know. I’ve seen this happen at the beginning of the reviewing process, but the more insidious case is when it happens at the end, where people are pressed for time and low quality judgements can become common.

An interesting approach for addressing the constraint objective would be optimizing a different objective, such as the product of affinities
rather than the sum. I’ve seen no experimentation of this sort.

For ICML, there are about 3 levels of “reviewer”: the program chair who is responsible for all papers, the area chair who is responsible for organizing reviewing on a subset of papers, and the program committee member/reviewer who has primary responsibility for reviewing. In 2012 tried to avoid these failure modes in a least-system effort way using a blended approach. We used bidding to get a higher quality affinity matrix. We used a constraint system to assign the first reviewer to each paper and two area chairs to each paper. Then, we asked each area chair to find one reviewer for each paper. This obviously dealt with the one-area-chair failure mode. It also helps substantially with low quality assignments from the constrained system since (a) the first reviewer chosen is typically higher quality than the last due to it being the least constrained (b) misassignments to area chairs are diagnosed at the beginning of the process by ACs trying to find reviewers (c) ACs can reach outside of the initial program committee to find reviewers, which existing automated systems can not do.

The next way that reviewing can go wrong is via biased reviewing.

  1. Author name bias is a famous one. In my experience it is real: well known authors automatically have their paper taken seriously, which particularly matters when time is short. Furthermore, I’ve seen instances where well-known authors can slide by with proof sketches that no one fully understands.
  2. Review anchoring is a very significant problem if it occurs. This does not happen in the standard review process, because the reviews of others are not visible to other reviewers until they are complete.
  3. A more subtle form of bias is when one reviewer is simply much louder or charismatic than others. Reviewing without an in-person meeting is actually helpful here, as it reduces this problem substantially.

Reviewing can also be low quality. A primary issue here is time: most reviewers will submit a review within a time constraint, but it may not be high quality due to limits on time. Minimizing average reviewer load is quite important here. Staggered deadlines for reviews are almost certainly also helpful. A more subtle thing is discouraging low quality submissions. My favored approach here is to publish all submissions nonanonymously after some initial period of time.

Another significant issue in reviewer quality is motivation. Making reviewers not anonymous to each other helps with motivation as poor reviews will at least be known to some. Author feedback also helps with motivation, as reviewers know that authors will be able to point out poor reviewing. It is easy to imagine that further improvements in reviewer motivation would be helpful.

A third form of low quality review is based on miscommunication. Maybe there is silly typo in a paper? Maybe something was confusing? Being able to communicate with the author can greatly reduce ambiguities.

The last problem is dictatorship at decision time for which I’ve seen several variants. Sometimes this comes in the form of giving each area chair a budget of papers to “champion”. Sometimes this comes in the form of an area chair deciding to override all reviews and either accept or more likely reject a paper. Sometimes this comes in the form of a program chair doing this as well. The power of dictatorship is often available, but it should not be used: the wiser course is keeping things representative.

At ICML 2012, we tried to deal with this via a defined power approach. When reviewers agreed on the accept/reject decision, that was the decision. If the reviewers disgreed, we asked the two area chairs to make decisions and if they agreed, that was the decision. It was only when the ACs disagreed that the program chairs would become involved in the decision.

The above provides an understanding of how to create a good reviewing process for a large conference. With this in mind, we can consider various proposals at the peer review workshop and elsewhere.

  1. Double Blind Review. This reduces bias, at the cost of decreasing reviewer motivation. Overall, I think it’s a significant long term positive for a conference as “insiders” naturally become more concerned with review quality and “outsiders” are more prone to submit.
  2. Better paper/reviewer matching. A pure win, with the only caveat that you should be familiar with failure modes and watch out for them.
  3. Author feedback. This improves review quality by placing a check on unfair reviews and reducing miscommunication at some cost in time.
  4. Allowing an appendix or ancillary materials. This allows authors to better communicate complex ideas, at the potential cost of reviewer time. A standard compromise is to make reading an appendix optional for reviewers.
  5. Open reviews. Open reviews means that people can learn from other reviews, and that authors can respond more naturally than in single round author feedback.

It’s important to note that none of the above are inherently contradictory. This is not necessarily obvious as proponents of open review and double blind review have found themselves in opposition at times. These approaches can be accommodated by simply hiding authors names for a fixed period of 2 months while the initial review process is ongoing.

Representative reviewing seems like the real difficult goal. If a paper is rejected in a representative reviewing process, then perhaps it is just not of sufficient interest. Similarly, if a paper is accepted, then perhaps it is of real and meaningful interest. And if the reviewing process is not representative, then perhaps we should fix the failure modes.

Edit: Crossposted on CACM.


ICML survey and comments

Just about nothing could keep me from attending ICML, except for Dora who arrived on Monday. Consequently, I have only secondhand reports that the conference is going well.

For those who are remote (like me) or after the conference (like everyone), Mark Reid has setup the ICML discussion site where you can comment on any paper or subscribe to papers. Authors are automatically subscribed to their own papers, so it should be possible to have a discussion significantly after the fact, as people desire.

We also conducted a survey before the conference and have the survey results now. This can be compared with the ICML 2010 survey results. Looking at the comparable questions, we can sometimes order the answers to have scores ranging from 0 to 3 or 0 to 4 with 3 or 4 being best and 0 worst, then compute the average difference between 2012 and 2010.

Glancing through them, I see:

  1. Most people found the papers they reviewed a good fit for their expertise (-.037 w.r.t 2010). Achieving this was one of our subgoals in the pursuit of high quality decisions.
  2. Most people had sufficient time for doing reviews. This was something that we worried about significantly in shifting the paper deadline and otherwise massaging the schedule. Most people also thought the review period was sufficiently long and most reviews were high quality (+.023 w.r.t. 2010)
  3. About 1/4 of reviewers say that author response changed their mind on a paper and 2/3 of reviewers say discussion changed their mind on a paper. The expectation of decision impact from author response is reduced from 2010 (-.135). The existence of author response is overwhelmingly preferred.
  4. People generally found ICML reviewing the same or better than previous ICMLs (+.35 w.r.t. 2010) and other similar conferences (+.198 w.r.t. 2010) at the cost of being somewhat more work. A substantial bump in reviewing quality was a primary goal.
  5. The ACs spent substantially more time (43 hours on average) than PC members (28 hours on average). This agrees with our expectation—the set of ACs didn’t change even after we had a 50% increase in submissions. The AC load we had this year was probably too high and will need to be reduced somewhat for next year.
  6. 2/3 of authors prefer the option to revise a paper during author response.
  7. The choice of how to deal with increased submissions is deeply undecided, with a slight preference for short talk+poster as we did.
  8. Most people like having two workshop days or don’t care.
  9. There is a strong preference for COLT and UAI colocation with the next tier of preference for IJCAI, KDD, AAAI, and CVPR.


ICML acceptance statistics

Tags: Conferences,Reviewing jl@ 8:24 pm

People are naturally interested in slicing the ICML acceptance statistics in various ways. Here’s a rundown for the top categories.

18/66 = 0.27 in (0.18,0.36) Reinforcement Learning
10/52 = 0.19 in (0.17,0.37) Supervised Learning
9/51 = 0.18 not in (0.18, 0.37) Clustering
12/46 = 0.26 in (0.17, 0.37) Kernel Methods
11/40 = 0.28 in (0.15, 0.4) Optimization Algorithms
8/33 = 0.24 in (0.15, 0.39) Learning Theory
14/33 = 0.42 not in (0.15, 0.39) Graphical Models
10/32 = 0.31 in (0.15, 0.41) Applications (+5 invited)
8/29 = 0.28 in (0.14, 0.41]) Probabilistic Models
13/29 = 0.45 not in (0.14, 0.41) NN & Deep Learning
8/26 = 0.31 in (0.12, 0.42) Transfer and Multi-Task Learning
13/25 = 0.52 not in (0.12, 0.44) Online Learning
5/25 = 0.20 in (0.12, 0.44) Active Learning
6/22 = 0.27 in (0.14, 0.41) Semi-Supervised Learning
7/20 = 0.35 in (0.1, 0.45) Statistical Methods
4/20 = 0.20 in (0.1, 0.45) Sparsity and Compressed Sensing
1/19 = 0.05 not in (0.11, 0.42) Ensemble Methods
5/18 = 0.28 in (0.11, 0.44) Structured Output Prediction
4/18 = 0.22 in (0.11, 0.44) Recommendation and Matrix Factorization
7/18 = 0.39 in (0.11, 0.44) Latent-Variable Models and Topic Models
1/17 = 0.06 not in (0.12, 0.47) Graph-Based Learning Methods
5/16 = 0.31 in (0.13, 0.44) Nonparametric Bayesian Inference
3/15 = 0.20 in (0.7, 0.47) Unsupervised Learning and Outlier Detection
7/12 = 0.58 not in (0.08, 0.50) Gaussian Processes
5/11 = 0.45 not in (0.09, 0.45) Ranking and Preference Learning
2/11 = 0.18 in (0.09, 0.45) Large-Scale Learning
0/9 = 0.00 in [0, 0.56) Vision
3/9 = 0.33 in [0, 0.56) Social Network Analysis
0/9 = 0.00 in [0, 0.56) Multi-agent & Cooperative Learning
2/9 = 0.22 in [0, 0.56) Manifold Learning
4/8 = 0.50 not in [0, 0.5) Time-Series Analysis
2/8 = 0.25 in [0, 0.5] Large-Margin Methods
2/8 = 0.25 in [0, 0.5] Cost Sensitive Learning
2/7 = 0.29 in [0, 0.57) Recommender Systems
3/7 = 0.43 in [0, 0.57) Privacy, Anonymity, and Security
0/7 = 0.00 in [0, 0.57) Neural Networks
0/7 = 0.00 in [0, 0.57) Empirical Insights
0/7 = 0.00 in [0, 0.57) Bioinformatics
1/6 = 0.17 in [0, 0.5) Information Retrieval
2/6 = 0.33 in [0, 0.5) Evaluation Methodology

Update: See Brendan’s graph for a visualization.

I usually find these numbers hard to interpret. At the grossest level, all areas have significant selection. At a finer level, one way to add further interpretation is to pretend that the acceptance rate of all papers is 0.27, then compute a 5% lower tail and a 5% upper tail. With 40 categories, we expect to have about 4 violations of tail inequalities. Instead, we have 9, so there is some evidence that individual areas are particularly hot or cold. In particular, the hot topics are Graphical models, Neural Networks and Deep Learning, Online Learning, Gaussian Processes, Ranking and Preference Learning, and Time Series Analysis. The cold topics are Clustering, Ensemble Methods, and Graph-Based Learning Methods.

We also experimented with AIStats resubmits (3/4 accepted) and NFP papers (4/7 accepted) but the numbers were to small to read anything significant.

One thing that surprised me was how uniform decisions were as a function of average score in reviews. All reviews included a decision from {Strong Reject, Weak Reject, Weak Accept, Strong Accept}. These were mapped to numbers in the range {1,2,3,4}. In essence, average review score < 2.2 meant 0% chance of acceptance, and average review score > 3.1 meant acceptance. Due to discretization in the number of reviewers and review scores there were only 3 typical uncertain outcomes:

  1. 2.33. This was either 2 Weak Rejects+Weak Accept or Strong Reject+2 Weak Accepts or (rarely) Strong Reject+Weak Reject+Strong Accept. About 8% of these paper were accepted.
  2. 2.67. This was either Weak Reject+Weak Accept*2 or Strong Accept+2 Weak Rejects or (rarely) Strong Reject+Weak Accept+Strong Accept. About 48% of these paper were accepted.
  3. 3.0. This was commonly 3 Weak Accepts or Strong Accept+Weak Accept+Weak Reject or (rarely) 2 Strong Accepts + Strong Reject. About 90% of these papers were accepted.

One question I’ve always wondered is: How much variance is there in the accept/reject decision? In general, correlated assignment of reviewers can greatly increase the amount of variance, so one of our goals this year was doing as independent an assignment as possible. If you accept that as independence, we essentially get 3 samples for each paper where the average standard deviation of reviewer scores before author feedback and discussion is 0.64. After author feedback and discussion the standard deviation drops to 0.51. If we pretend that papers have an intrinsic value between 1 and 4 then think of reviews as discretized gaussian measurements fed through the above decision criteria, we get the following:

There are great caveats to this picture. For example, treating the AC’s decision as random conditioned on the reviewer average is a worst-case analysis. The reality is that ACs are removing noise from the few events that I monitored carefully, although it is difficult to quantify this. Similarly, treating the reviews observed after discussion as independent is clearly flawed. A reasonable way to look at it is: author feedback and discussion get us about 1/3 or 1/4 of the way to the final decision from the initial reviews.

Conditioned on the papers, discussion, author feedback and reviews, AC’s are pretty uniform in their decisions with ~30 papers where ACs disagreed on the accept/reject decision. For half of those, the ACs discussed further and agreed, leaving Joelle and I a feasible quantity of cases to look at (plus several other exceptions).

At the outset, we promised a zero-spof reviewing process. We actually aimed higher: at least 3 people needed to make a wrong decision for the ICML 2012 reviewing process to kick out a wrong decision. I expect this happened a few times given the overall level of quality disagreement and quantities involved, but hopefully we managed to reduce the noise appreciably.


ICML: Behind the Scenes

This is a rather long post, detailing the ICML 2012 review process. The goal is to make the process more transparent, help authors understand how we came to a decision, and discuss the strengths and weaknesses of this process for future conference organizers.

Microsoft’s Conference Management Toolkit (CMT)
We chose to use CMT over other conference management software mainly because of its rich toolkit. The interface is sub-optimal (to say the least!) but it has extensive capabilities (to handle bids, author response, resubmissions, etc.), good import/export mechanisms (to process the data elsewhere), excellent technical support (to answer late night emails, add new functionalities). Overall, it was the right choice, although we hope a designer will look at that interface sometime soon!

Toronto Matching System (TMS)
TMS is now being used by many major conferences in our field (including NIPS and UAI). It is an automated system (developed by Laurent Charlin and Rich Zemel at U. Toronto) to match reviewers to papers, based on an analysis of each reviewer’s publications. TMS collects publications from reviewers, parses them into features and applies unsupervised or supervised learning techniques to predict the relevance of any target paper for any reviewer. We convinced TMS to integrate with CMT and funded Laurent’s work for that. Reviewers were asked to put in a publication list for TMS to parse. For those who failed to do so (after many reminders!), we manually added that information from public sources.

The Program Committee
Recruiting a program committee that is both large and highly qualified is difficult these days. We sent out 69 area chair invitations; 50 (highly qualified!) people accepted. Each of these area chairs was asked to nominate a list of potential reviewers. We sent out approximately 700 invitations for program committee members; 389 accepted. A number of additional PC members were recruited during the review process (most of them for 1-2 papers), for a total of 470 active PC members. In terms of seniority, the final PC contains about ~15% students, 80% researchers, 5% other.

The Surge (ICML + 50%)
The first big challenge came on the submission deadline. In the past few years, ICML had consistently received ~550-600 submissions. This year, we had a 50% increase, to 890 submissions. We had recruited a PC that could comfortably handle 700 papers. Dealing with an extra 200 papers was not an easy task.

About 10 submissions were rejected without review for various reasons (severe formatting issues, extra pages, non-anonymization).

An unsupervised version of TMS was used to generate a list of candidate papers for each reviewer and area chair. This was done working closely with the Laurent Charlin of TMS using validation on previous NIPS data. CMT did not have the functionality to show a good list of candidate papers to reviewers, so we crafted an interface to show this list and let reviewers use that in conjunction with CMT. Ideally, this will be better incorporated in CMT in the future.

When you ask a group of scientists to run a conference, you must expect a few experiments will take place…. And so we decided to assess the usefulness of TMS scoring for generating lists of papers to bid on. To do this, we (randomly) assigned PC members to 1 of 3 groups. One group saw a list purely based on TMS scores. Another group received a list based on the matching between their subject area and that of the paper (referred to as the “relevance” score in CMT). The third group received a list based on a mix of both TMS and relevance. Reviewers were allowed to bid on any paper (excluding those with which they had a conflict); the lists were provided to help them efficiently sort through the large number of papers. We then compared the set of bids for a reviewer, with the list of suggestions, and measured the correspondence.

The following is the Discounted Cumulative Gain (DCG) of each list with respect to the bidding scores, averaged separately for each group. Note that each group was only presented with their corresponding list and not the others.

Group: CMT Group: TMS Group: CMT+TMS
Sorting by CMT scores 6.11 out of 12.64 (48%) 4.98 out of 13.63 (36%) 4.87 out of 13.55 (35%)
Sorting by TMS score 4.06 out of 12.64 (32%) 6.43 out of 13.63 (47%) 5.72 out of 13.55 (42%)
Sorting by TMS+CMT 4.77 out of 12.64 (37%) 6.11 out of 13.63 (44%) 6.71 out of 13.55 (49%)

A micro-survey was also run to collect further information on how users liked their short list. 85% of the participants indicated that they have used the list interface provided to them. The following is the preference indicated by each group (~75 reviewers in each group, ~2% error):

Preferred CMT over list 15% 12% 8%
Preferred list+CMT 81% 83% 83%
Preferred list over CMT 4% 5% 9%

It is obvious from the above that most participants found the list useful in conjunction with CMT (suggesting that the list should be integrated inside CMT). We can also see that those who were presented with a list based on TMS scores were more likely to find the list useful.

Note that all of the above was done in a long hectic but fun weekend.

Imputing Missing Bids
CMT assumes that the reviewers are not willing to review a paper unless stated otherwise. It does not differentiate between an unseen (but potentially relevant) paper and a paper that has been seen and ignored. This is a real shortcoming when it comes to matching papers to reviewers, especially for those reviewers that did not bid often. To mitigate this problem, we used the click information on the shortlist presented to the reviewers to find out which papers have been observed and ignored. We then impute these cases as real non-willing bids.

Around 30 reviewers did not provide any bids (and many had only a few). This is problematic because the tools used to do the actual reviewer-paper matching tend to assign the papers without any bids to the reviewers who did not bid, regardless of the match in expertise.

Once the bidding information was in and imputation was done, we now had to fill in the rest of the paper-reviewer bidding matrix to mitigate the problem with sparse bidders. This was done, once again, through TMS, but this time using a supervised learning approach.

Using supervised learning was more delicate than expected. To deal with the wildly varying number of bids per person, we imputed zero bids, first from papers that were plausibly skipped over, and if necessary at random from papers not bid on such that each person had the same expected bid in the dataset. From this dataset, we held out a random bid per person, and then trained to predict well the heldout bid. Most optimization approaches performed poorly due to the number of features greatly exceeding the number of labels. The best approach we found used the online algorithms in Vowpal Wabbit with a mass personalized training method similar to the one discussed here. This trained predictor was used to predict bid values for the full paper-reviewer bid matrix.

Automated Area Chair and First Reviewer Assignment
Once we had the imputed paper-reviewer bidding matrix, CMT was used to generate the actual match between papers and area chairs, and (separately) between papers and reviewers. Each paper had two area chairs (sometimes called “meta-reviewers” in CMT) assigned to it, one primary, one secondary, by running two rounds of assignments (so that the primary was usually the “better” match). One reviewer per paper was also assigned automatically by CMT in a similar fashion. CMT provides proper load balancing, so that all area chairs and reviewers had similar loads.

Manual Checks of the Automated Assignments
Before finalizing the automated assignment, we manually looked through the list of papers to fix any potential problems that were not handled by the automated process. The two major cases were papers that did not go through the TMS system (authors did not agree to do so), and cases of poor primary-secondary meta-reviewer pairs (when the two area chairs are judged to be too close to offer independent assessment, e.g. working at the same institution, previous supervisor-student relationship).

Second and Third Reviewer Assignment
Once the initial assignments were announced, we asked the two area chairs for a given paper to each manually assign another reviewer from the PC. To help area chairs with this, we generated a shortlist of 10 recommended reviewers for each paper (using the estimated bid matrix and TMS score, with the CMT matching algorithm for load balancing of reviewer suggestions.) Area chairs were free to either use this list, or select from the complete program committee, or alternately, they could seek an outside reviewer which was then added to the PC, an option used 80 times. The load for each reviewer was restricted to at most 7 papers with exceptions when they agreed explicitly to more.

The second and third uses of TMS, including the new supervised learning system, lead to another long hectic weekend with Laurent, Mahdi, Joelle, and John all deeply involved.

Most papers received at least 3 full reviews in the first round. Reviewers could not see each others’ reviews until they submitted their own. ML-Journaled submissions (see double submission guide) were reviewed only by two area chairs. In a small number of regular submissions (less than 10), we received 2 very negative reviews and notified the third reviewer (who was usually late by this point!) that we would not need their review.

Authors’ Response
Authors were given a chance to respond to the reviews during a short feedback period. This is becoming a standard practice in machine learning conferences. Authors were also allowed to upload a new version of the paper. The motivation here is that in some cases, it is easier to show the changes directly in the paper, rather than discuss them separately.

Our analysis shows that authors’ responses and subsequent discussions by reviewers made significant changes to the scoring of papers. A total of ~35% of the papers had some change in their scores after the author feedback. The average score for ~50% of the papers went down, stayed the same for ~10%, and went up for the other ~40%. The variance on the scores decreased by ~20%, indicating some convergence in the decisions.

Final Decisions
To help us better decide on the quality of the papers, we asked the primary area chairs to provide a meta-review for each of their papers. For papers without unanimous review decisions (i.e. some reviews wanted to accept and some wanted to reject), we asked the secondary area chair to (independently) fill-in a meta-review, recommending whether to accept or reject the paper. A total of 1214 meta-reviews were provided. There were also 20 papers for which a 4th review was added in this period.

In all cases where the primary and secondary area chairs disagreed on the decision, the program chairs were directly involved, reviewing all the evidence (reviews, rebuttal, discussion, often the paper itself), and entering in a discussion (usually via email) with the area chairs, until a unanimous decision was achieved.
A total of 243 papers (27% of submissions) were accepted. Author notifications were sent out on April 30.


Compassionate Reviewing

Most long conversations between academics seem to converge on the topic of reviewing where almost no one is happy. A basic question is: Should most people be happy?

The case against is straightforward. Anyone who watches the flow of papers realizes that most papers amount to little in the longer term. By it’s nature research is brutal, where the second-best method is worthless, and the second person to discover things typically gets no credit. If you think about this for a moment, it’s very different from most other human endeavors. The second best migrant laborer, construction worker, manager, conductor, quarterback, etc… all can manage quite well. If a reviewer has even a vaguely predictive sense of what’s important in the longer term, then most people submitting papers will be unhappy.

But this argument unravels, in my experience. Perhaps half of reviews are thoughtless or simply wrong with a small part being simply malicious. And yet, I’m sure that most reviewers genuinely believe they can predict what will and will not be useful in the longer term. This disparity is a lack of communication. When academics have conversations about reviewing, the presumption of participants in each conversation is that they all share about the same beliefs about what will be useful, and what will take off. Such conversations rarely go into specifics, because the specifics are boring in particular, technical, and because their is a real chance of disagreement on the specifics themselves.

When double blind reviewing was first being considered for ICML, I remember speaking about the experience in the Crypto community, where in my estimate the reviewing was both fairer and less happy. Many conferences in machine learning have shifted to doubleblind reviewing, and I think we have seen this come to pass here as well. Without double blind reviewing, it is common to have an “in” crowd who everyone respects and whose papers are virtually always accepted. These people are happy, and the rest have little voice. With double blind reviewing, everyone suffers substantial rejections.

We might say “fine, at least it’s fair”, but in my experience there is a real problem. From a viewpoint external to the community, when the reviewing is poor and the viewpoint of people in the community highly contradictory, nothing good happens. Outsiders (i.e. most people) viewing the acrimony choose some other way to solve problems, proposals don’t get funded, and the community itself tends to fracture. For example, in cryptography, TCC (not double blind) has started, presumably because the top theory people got tired of having their papers rejected at Crypto (double blind). From a process-of-research standpoint, this seems suboptimal, as different groups using different methods to solve similar problems are particularly the people who you would prefer talking to each other.

What seems to be lost with double blind reviewing is some amount of compassion, unfairly allocated. In a double blind system, any given paper is plausibly from someone you don’t know, and since most papers go nowhere, plausibly not going anywhere. Consequently, the bias starts “against” for all work, a disadvantage which can be quite difficult to overcome. Some time ago, I discussed how I thought motivation should be the responsibility of the reviewer. Aaron Hertzman strongly disagreed on the grounds that this belief could dead end your career as an author. I’ve come to appreciate his viewpoint to an extent. But, it misses the point slightly—the question of “What is good for the community?” differs from “What is good for the author?” In a healthy community, reviewers will actively understand why a piece of work is or is not important, filling in and extending the motivation as they consider the problem.

So, a question is: How can we get compassionate reviewing? (And in a fair way?) It might help somewhat for reviewers to actively consider, as part of their review, the level and mechanism of impact that a paper may have. Reducing reviewing load is certainly helpful, but it is not sufficient alone, because many people naturally interpret a reduced reviewing load as time to work on other things. And, some mechanisms seem to even harm. For example, the two-phase reviewing process that ICML currently uses might save 0.5 reviews/paper, while guaranteeing that for half of the papers, the deciding review is done hastily with no author feedback, a recipe for mistakes.

What creates a great deal of compassion? Public responsibility helps (witness workshops more interesting than conferences). A natural conversation helps (the current method of single round response tends to be very stilted). And time, of course, helps. What else?


Future Publication Models @ NIPS

Yesterday, there was a discussion about future publication models at NIPS. Yann and Zoubin have specific detailed proposals which I’ll add links to when I get them (Yann’s proposal and Zoubin’s proposal).

What struck me about the discussion is that there are many simultaneous concerns as well as many simultaneous proposals, which makes it difficult to keep all the distinctions straight in a verbal conversation. It also seemed like people were serious enough about this that we may see some real movement. Certainly, my personal experience motivates that as I’ve posted many times about the substantial flaws in our review process, including some very poor personal experiences.

Concerns include the following:

  1. (Several) Reviewers are overloaded, boosting the noise in decision making.
  2. (Yann) A new system should run with as little built-in delay and friction to the process of research as possible.
  3. (Hanna Wallach(updated)) Double-blind review is particularly important for people who are unknown or from an unknown institution.
  4. (Several) But, it’s bad to take double blind so seriously as to disallow publishing on arxiv or personal webpages.
  5. (Yann) And double-blind is bad when it prevents publishing for substantial periods of time. Apparently, this comes up in CVPR.
  6. (Zoubin) Any new system should appear to outsiders as if it’s the old system, or a journal, because it’s already hard enough to justify CS tenure cases to other disciplines.
  7. (Fernando) There shouldn’t be a big change with a complex bureaucracy, but rather a smaller changes which are obviously useful or at least worth experimenting with.

There were other concerns as well, but these are the ones that I remember.

Elements of proposals include:

  1. (Yann) Everything should go to Arxiv or an arxiv-like system first, as per physics or mathematics. This addresses (1), because it delinks dissemination from review, relieving some of the burden of reviewing. It also addresses (2) since with good authors they can immediately begin building on each other’s work. It conflicts with (3), because Arxiv does not support double-blind submission. It does not conflict if we build our own system.
  2. (Fernando) Create a conference coincident journal in which people can publish at any time. VLDB has apparently done this. It can be done smoothly by allowing submission in either conference deadline mode or journal mode. This proposal addresses (1) by reducing peak demand on reviewing. It also addresses (6) above.
  3. (Daphne) Perhaps we should have a system which only reviews papers for correctness, which is not nearly as subjective as for novelty or interestingness. This addresses (1), by eliminating some concerns for the reviewer. It is orthogonal to the double blind debate. In biology, such a journal exists (pointer updated), because delays were becoming absurd and intolerable.
  4. (Yann) There should be multiple publishing entities (people or groups of people) that can bless a paper as interesting. This addresses (1).

There are many other proposal elements (too many for my memory), which hopefully we’ll see in particular proposals. If other people have concrete proposals, now is probably the right time to formalize them.


Decision by Vetocracy

Few would mistake the process of academic paper review for a fair process, but sometimes the unfairness seems particularly striking. This is most easily seen by comparison:

Paper Banditron Offset Tree Notes
Problem Scope Multiclass problems where only the loss of one choice can be probed. Strictly greater: Cost sensitive multiclass problems where only the loss of one choice can be probed. Often generalizations don’t matter. That’s not the case here, since every plausible application I’ve thought of involves loss functions substantially different from 0/1.
What’s new Analysis and Experiments Algorithm, Analysis, and Experiments As far as I know, the essence of the more general problem was first stated and analyzed with the EXP4 algorithm (page 16) (1998). It’s also the time horizon 1 simplification of the Reinforcement Learning setting for the random trajectory method (page 15) (2002). The Banditron algorithm itself is functionally identical to One-Step RL with Traces (page 122) (2003) in Bianca‘s thesis with the epsilon greedy strategy and a multiclass perceptron with update scaled by the importance weight.
Computational Time O(k) per example where k is the number of choices O(log k) per example Lower bounds on the sample complexity of learning in this setting are a factor of k worse than for supervised learning, implying that many more examples may be needed in practice. Consequently, learning algorithm speed is more important than in standard supervised learning.
Analysis Incomparable. An online regret analysis showing that if a small hinge loss predictor exists, a bounded number of mistakes occur. Also, an algorithm independent analysis of the fully realizable case. Incomparable. A learning reduction analysis showing how the regret of any base classifier bounds policy regret. Also contains a lower bound and comparable analysis of all plausible alternative reductions.
Experiments 1 dataset, comparing with no other approaches to solving the problem. 13 datasets, comparing with 2 other approaches to solve the problem.
Outcome Accepted at ICML Rejected at ICML, NIPS, UAI, and NIPS.

The reviewers of the Banditron paper made the right call. The subject is interesting, and analysis of a new learning domain is of substantial interest. Real advances in machine learning often come as new domains of application. The talk was well attended and generated substantial interest. It’s also important to remember the reviewers of the two papers probably did not overlap, so there was no explicit preference for A over B.

Why was the Offset Tree rejected? One of these rejections is easily explained as a fluke—we ran into a reviewer at UAI who believes that learning by memorization is the way to go. I, and virtually all machine learning people, disagree but some reviewers at UAI aren’t interested or expert in machine learning.

The striking thing about the other 3 rejects is that they all contain a reviewer who doesn’t read the paper. Instead, the reviewer asserts that learning reductions are bogus because for an alternative notion of learning reduction, made up by the reviewer, an obviously useless approach yields a factor of 2 regret bound. I believe this is the same reviewer each time, because the alternative theorem statement drifted over the reviews fixing bugs we pointed out in the author response.

The first time we encountered this review, we assumed the reviewer was just cranky that day—maybe we weren’t quite clear enough in explaining everything as it’s always difficult to get every detail clear in new subject matter. I have sometimes had a very strong negative impression of a paper which later turned out to be unjustified upon further consideration. Sometimes when a reviewer is cranky, they change their mind after the authors respond, or perhaps later, or perhaps never but you get a new set of reviewers the next time.

The second time the review came up, we knew there was a problem. If we are generous to the reviewer, and taking into account the fact that learning reduction analysis is a relatively new form of analysis, the fear that because an alternative notion of reduction is vacuous our notion of reduction might also be vacuous isn’t too outlandish. Fortunately, there is a way to completely address that—we added an algorithm independent lower bound to the draft (which was the only significant change in content over the submissions). This lower bound conclusively proves that our notion of learning reduction is not vacuous as is the reviewer’s notion of learning reduction.

The review came up a third time. Despite pointing out the lower bound quite explicitly, the reviewer simply ignored it. This more-or-less confirms our worst fears. Some reviewer is bidding for the paper with the intent to torpedo review it. They are uninterested in and unwiling to read the content itself.

Shouldn’t author feedback address this? Not if the reviewer ignores it.

Shouldn’t Double Blind reviewing help? Not if the paper only has one plausible source. The general problem area and method of analysis were freely discussed on We withheld public discussion of the algorithm itself for much of the time (except for a talk at CMU) out of respect for the review process.

Why doesn’t the area chair/program chair catch it? It took us 3 interactions to get it, so it seems unrealistic to expect someone else to get it in one interaction. In general, these people are strongly overloaded and the reviewer wasn’t kind enough to boil down the essence of the stated objection as I’ve done above. Instead, they phrase it as an example and do not clearly state the theorem they have in mind or distinguish the fact that the quantification of that theorem differs from the quantification of our theorems. More generally, my observation is that area chairs rarely override negative reviews because:

  1. It risks their reputation since defending a criticized work requires the kind of confidence that can only be inspired by a thorough personal review they don’t have time for.
  2. They may offend the reviewer they invited to review and personally know.
  3. They figure that the average review is similar to the average perception/popularity by the community anyways.
  4. Even if they don’t agree with the reviewer, it’s hard to fully discount the review in their consideration.

I’ve seen these effects create substantial mental gymnastics elsewhere.

Maybe you just ran into a cranky reviewer 3 times randomly Maybe so. However, the odds seem low enough and the 1/2 year cost of getting another sample high enough, that going with the working hypothesis seems indicated.

Maybe the writing needs improving. Often that’s a reasonable answer for a rejection, but in this case I believe not. We’ve run the paper by several people, who did not have substantial difficulties understanding it. They even understand the draft well enough to make a suggestion or two. More generally, no paper is harder to read than the one you picked because you want to reject it.

What happens next? With respect to the Offset Tree, I’m hopeful that we eventually find reviewers who appreciate an exponentially faster algorithm, good empirical results, or the very tight and elegant analysis, or even all three. For the record, I consider the Offset Tree a great paper. It remains a substantial advance on the state of the art, even 2 years later, and as far as I know the Offset Tree (or the Realizable Offset Tree) consistently beat all reasonable contenders both in prediction and computational performance. This is rare and precious, as many papers tradeoff one for the other. It yields a practical algorithm applicable to real problems. It substantially addresses the RL to classification reduction problem. It also has the first nonconstant algorithm independent lower bound for learning reductions.

With respect to the reviewer, I expect remarkably little. The system is designed to protect reviewers, so they have virtually no responsibility for their decisions. This reviewer has a demonstrated capability to sabotage the review process at ICML and NIPS and a demonstrated willingness to continue doing so indefinitely. The process of bidding for papers and making up reasons to reject them seems tedious, but there is no fundamental reason why they can’t continue doing so for several decades if they remain active in academia.

This experience has substantially altered my understanding and appreciation of the review process at conferences. The bidding mechanism commonly used, coupled with responsibility-free reviewing is an invitation to abuse. A clever abusive reviewer can sabotage perhaps 5 papers per conference (out of 8 reviewed), while maintaining a typical average score. While I don’t believe most people choose papers with intent to sabotage, the capability is there and used by at least one person and possibly others. If, for example, 5% of reviewers are willing to abuse the process this way and there are 100 reviewers, every paper must survive 5 vetoes. If there are 200 reviewers, every paper must survive 10 vetoes. And if there are 400 reviewers, every paper must survive 20 vetoes. This makes publishing any paper that offends someone difficult. The surviving papers are typically inoffensive or part of a fad strong enough that vetoes are held back. Neither category is representative of high quality decision making. These observations suggest that the conference with the most reviewers tend strongly toward faddy and inoffensive papers, both of which often lack impact in the long term. Perhaps this partly explains why NIPS is so weak when people start citation counting. Conversely, this would suggest that smaller conferences and workshops have a natural advantage. Similarly, the reviewing style in theory conferences seems better—the set of bidders for any paper is substantially smaller, implying papers must survive fewer vetos.

This decision making process can be modeled as a group of n decision makers, each of which has the opportunity to veto any action. When n is relatively small, this decision making process might work ok, depending on the decision makers, but as n grows larger, it’s difficult to imagine a worse decision making process. The closest representatives outside of academia I know are deeply bureacratic governments and other large organizations where many people must sign off on something before it takes place. These vetocracies are universally frustrating to interact with. A reasonable conjecture is that any decision making process with a large veto number has poor characteristics.

A basic question is: Is a vetocracy inevitable for large organizations? I believe the answer is no. The basic observation is that the value of n can be logarithmic in the number of participants in an organization rather than linear, as per reviewing under a bidding process. An essential force driving vetocracy creation is a desire to offload responsibility for decisions, so there is no clear decision maker. A large organization not deciding by vetocracy must have a very different structure, with clearly dilineated responsibility.

NIPS provides an almost perfect natural experiment in it’s workshop organization, which involves the very same community of people and subject matter, yet works in a very different manner. There are one or two workshop chairs who are responsible for selecting amongst workshop proposals, after which the content of the workshop is entirely up to the workshop organizers. If a workshop is rejected, it’s clear who is at fault, and if a workshop presentation is rejected, it is often clear by who. Some workshop chairs use a small set of reviewers, but even then the effective veto number remains small. Similarly, if a workshop ends up a flop, it’s relatively easy to see who to blame—either the workshop chair for not predicting it, or the organizers for failing to organize. I can’t think of a single time when I attended both the workshops and the conference that the workshops were less interesting than the conference. My understanding is that this observation is common. Given this discussion, it will be particularly interesting to see how the review process Michael and Leon setup for ICML this year pans out, as it is a system with notably more responsibility assignment than in previous years.

Journals end up looking relatively good with respect to vetocracy avoidance. The ones I’m familiar with have a chief editor who bears responsibility for routing papers to an action editor, who bears responsibility for choosing good reviewers. Every agent except the reviewers is often known by the authors, and the reviewers don’t act as additional vetoers in nearly as strong a manner as reviewers with the opportunity to bid.

This experience has also altered my view of blogging and research. On one hand, I’m very enthusiastic about research in general, and my research in particular, where we are regularly cracking conventionally impossible problems. On the other hand, it seems that some small number of people viewing a discussion silently decide they don’t like it, and veto it given the opportunity. It only takes one to turn strong paper into a years-long odyssey, so public discussion of research directions and topics in a vetocracy is akin to voluntarily wearing a “kick me” sign. While this a problem for me, I expect it to be even worse for the members of a vetocracy in the long term.

It’s hard to imagine any research community surviving without a serious online presence. When a prospective new researcher looks around at existing research, if they don’t find serious online discussion, they’ll assume it doesn’t exist under the “not on the internet so it doesn’t exist” principle. This will starve a field of new people. More generally, there is an opportunity to get feedback about research directions and problems much more rapidly than is otherwise possible, allowing us to avoid research on dead end topics which are pervasive. At some point, it may even seem that people not willing to discuss their research simply avoid doing so because it is critically lacking in one way or another. Since a vetocracy creates a substantial disincentive to discuss research directions online, we can expect that communities sticking with decision by vetocracy to be at a substantial disadvantage.


Adversarial Academia

One viewpoint on academia is that it is inherently adversarial: there are finite research dollars, positions, and students to work with, implying a zero-sum game between different participants. This is not a viewpoint that I want to promote, as I consider it flawed. However, I know several people believe strongly in this viewpoint, and I have found it to have substantial explanatory power.

For example:

  1. It explains why your paper was rejected based on poor logic. The reviewer wasn’t concerned with research quality, but rather with rejecting a competitor.
  2. It explains why professors rarely work together. The goal of a non-tenured professor (at least) is to get tenure, and a case for tenure comes from a portfolio of work that is undisputably yours.
  3. It explains why new research programs are not quickly adopted. Adopting a competitor’s program is impossible, if your career is based on the competitor being wrong.

Different academic groups subscribe to the adversarial viewpoint in different degrees. In my experience, NIPS is the worst. It is bad enough that the probability of a paper being accepted at NIPS is monotonically decreasing in it’s quality. This is more than just my personal experience over a number of years, as it’s corroborated by others who have told me the same. ICML (run by IMLS) used to have less of a problem, but since it has become more like NIPS over time, it has inherited this problem. COLT has not suffered from this problem as much in my experience, although it had other problems related to the focus being defined too narrowly. I do not have enough experience with UAI or KDD to comment there.

There are substantial flaws in the adversarial viewpoint.

  1. The adversarial viewpoint makes you stupid. When viewed adversarially, any idea has crippling disadvantages and no advantages. Contorting your viewpoint enough to make this true damages your ability to conduct research. In short, it promotes poor mental hygiene.
  2. Many activities become impossible. Doing research is in general extremely hard, so there are many instances where working with other people can allow you to do things which are otherwise impossible.
  3. The previous two disadvantages apply even more strongly for a community—good ideas are more likely to be missed, change comes slowly, and often with steps backward.
  4. At it’s most basic level, the assumption that research is zero-sum is flawed, because the process of research is not done in a closed system. If the rest of society at large discovers that research is valuable, then the budget increases.

Despite these disadvantages, there is a substantial advantage as well: you can materially protect and aid your career by rejecting papers, preventing grants, and generally discriminating against key people doing interesting but competitive work.

The adversarial viewpoint has a validity in proportion to the number of people subscribing to it. For those of us who would like to deemphasize the adversarial viewpoint, what’s unclear is: how?

One concrete thing is: use Arxiv. For a long time, physicists have adopted an Arxiv-first philosophy, which I’ve come to respect. Arxiv functions as a universal timestamp which decreases the power of an adversarial reviewer. Essentially, you avoid giving away the power to muddy the track of invention. I’m expecting to use Arxiv for essentially all my past-but-unpublished and future papers.

It is plausible that limiting the scope of bidding, as Andrew McCallum suggested at the last ICML, and as is effectively implemented at this ICML, will help. The system of review at journals might also help for the same reason. In my experience as an author, if an anonymous reviewer wants to kill a paper they usually succeed. Most area chairs or program chairs are more interested in avoiding conflict with the reviewer (who they picked and may consider a friend) than reading the paper to determine the illogic of the review (which is a difficult task that simply cannot be done for all papers). NIPS experimented with a reputation system for reviewers last year, but I’m unclear on how well it worked, as an author’s score for a review and a reviewer’s score for the paper may be deeply correlated, revealing little additional information.

Public discussion of research can help with this, because very poor logic simply doesn’t stand up under public scrutiny. While I hope to nudge people in this direction, it’s clear that most people aren’t yet comfortable with public discussion.


Who is Responsible for a Bad Review?

Although I’m greatly interested in machine learning, I think it must be admitted that there is a large amount of low quality logic being used in reviews. The problem is bad enough that sometimes I wonder if the Byzantine generals limit has been exceeded. For example, I’ve seen recent reviews where the given reasons for rejecting are:

  1. [NIPS] Theorem A is uninteresting because Theorem B is uninteresting.
  2. [UAI] When you learn by memorization, the problem addressed is trivial.
  3. [NIPS] The proof is in the appendix.
  4. [NIPS] This has been done before. (… but not giving any relevant citations)

Just for the record I want to point out what’s wrong with these reviews. A future world in which such reasons never come up again would be great, but I’m sure these errors will be committed many times more in the future.

  1. This is nonsense. A theorem should be evaluated based on it’s merits, rather than the merits of another theorem.
  2. Learning by memorization requires an exponentially larger sample complexity than many other common approaches that often work well. Consequently, what is possible under memorization does not have any substantial bearing on common practice or what might be useful in the future.
  3. Huh? Other people, thank you for putting the proof in the appendix, so the paper reads better. It seems absurd to base a decision on the placement of the content rather than the content.
  4. This is a red flag for a bogus review. Every time I’ve seen a review (as an author or a fellow reviewer) where such claims are made without a concrete citation, they are false. Often they are false even when concrete citations are given.

A softer version of (4) is when someone is cranky because their own paper wasn’t cited. This is understandable, but a more appropriate response seems to be pointing things out, and reviewing anyways. This avoids creating the extra work (for authors and reviewers) of yet another paper resubmission, and reasonable authors do take such suggestions into account.

NIPS figures fairly prominently here. While these are all instances in the last year, my experience after interacting with NIPS for almost a decade is that the average quality of reviews is particularly low there—in many instances reviewers clearly don’t read the papers before writing the review. Furthermore, such low quality reviews are often the deciding factor for the paper decision. Blaming the reviewer seems to be the easy solution for a bad review, but a bit more thought suggests other possibilities:

  1. Area Chair In some conferences an “area chair” or “senior PC” makes or effectively makes the decision on a paper. In general, I’m not a fan of activist area chairs, but when a reviewer isn’t thinking well, I think it is appropriate to step in. This rarely happens, because the easy choice is to simply accept the negative review. In my experience, many Area Chairs are eager to avoid any substantial controversy, and there is a general tendency to believe that something must be wrong with a paper that has a negative review, even if it isn’t what was actually pointed out.
  2. Program Chair In smaller conferences, Program Chairs play the same role as the area chair, so all of the above applies, except now you know the persons name explicitly making them easier to blame. This is a little bit too tempting, I think. For example, I know David McAllester understands that learning by memorization is a bogus reference point, and probably he was just too busy to really digest the reviews. However, a Program Chair is responsible for finding appropriate reviewers for papers, and doing so (or not) has a huge impact on whether a paper is accepted. Not surprisingly, if a paper about the sample complexity of learning is routed to people who have never seen a proof involving sample complexity before, the reviews tend to be spuriously negative (and the paper unread).
  3. Author A reviewer might blame an author, if it turns out later that the reasons given in the review for rejection were bogus. This isn’t absurd—writing a paper well is hard and it’s easy for small mistakes to be drastically misleading in technical content.
  4. Culture A conference has a culture associated with it that is driven by the people who keep coming back. If in this culture it is considered ok to do all the reviews on the last day, it’s unsurprising to see reviews lacking critical thought that could be written without reading the paper. Similarly, it’s unsurprising to see little critical thought at the area chair level, or in the routing of papers to reviewers. This answer is pretty convincing: it explains why low quality reviews keep happening year after year at a conference.

If you believe the Culture reason, then what’s needed is a change in the culture. The good news is that this is both possible and effective. There are other conferences where reviewers expect to spend several hours reviewing a paper. In my experience this year, it was true of COLT and for my corner of SODA. Effecting the change is simply a matter of community standards, and that is just a matter of leaders in the community leading.


The SODA Program Committee

Tags: Conferences,Reviewing ,Theory jl@ 7:10 am

Claire asked me to be on the SODA program committee this year, which was quite a bit of work.

I had a relatively light load—merely 49 theory papers. Many of these papers were not on subjects that I was expert about, so (as is common for theory conferences) I found various reviewers that I trusted to help review the papers. I ended up reviewing about 1/3 personally. There were a couple instances where I ended up overruling a subreviewer whose logic seemed off, but otherwise I generally let their reviews stand.

There are some differences in standards for paper reviews between the machine learning and theory communities. In machine learning it is expected that a review be detailed, while in the theory community this is often not the case. Every paper given to me ended up with a review varying between somewhat and very detailed.

I’m sure not every author was happy with the outcome. While we did our best to make good decisions, they were difficult decisions to make. For example, if there is a well written paper on an interesting topic which analyzes a flawed abstraction of the topic, should it get in? I would rate this a ‘weak accept’.

Here are some observations/thoughts about the process (Several also appear in Claire’s report).

  1. Better feedback isn’t too hard. The real time sink in reviewing a theory paper is reading it. Leaving a few comments, even if just “I don’t like the model analyzed because it misses important feature X.” is relatively easy. My impression of the last COLT was that COLT had entirely switched from minimal author feedback to substantial author feedback. This year’s SODA was somewhere inbetween, depending on the PC member involved, which is a definite trend towards stronger comments for SODA.
  2. Normalization There were very substantial differences amongst the PC members in what fraction of papers they wanted to accept, and this leaked into the final decisions. Normalizing reviewer ratings is standard operating procedure at some machine learning conferences, so I helped with that. Even with that help, further efforts at normalization in the future seem like they could help, for example in getting the decision on the paper above right.
  3. Ordering There were various areas where we tried to order all the reasonable papers and make a decision based on the ordering. Where the papers are sufficiently related, I think this is very helpful, and the act even changed my opinion on some papers a bit by putting them in better context. Not everyone imposed the same ordering, because there are somewhat different tastes: Do you care about the techniques used? (A traditional theory concern) or about the quality of the result? (I’m more focused here.) Nevertheless, it helped reduce the noise. Incidentally, there is substantial theoretical evidence that decisions by ordering are more robust than decisions by absolute score producing an ordering.
  4. Writing quality I was surprised by the poor writing quality of some SODA papers—several were basically not readable without a thorough understanding of referenced papers, and a substantial ability to infer what was meant rather than what was said. Some of these papers were accepted, which would have been impossible in a conference with double-blind reviewing.
  5. PC size The tradition in theory conferences is to have a relatively small program committee. I don’t see much advantage to this for SODA. The program committe is small enough and SODA is broad enough that it seems dubious to claim that every PC member is an expert on the subject of all of their papers. Also, (frankly) the highest quality reviews from my batch of papers weren’t written by me, but rather by reviewers that I picked who had the time to really grind through all the nitty-gritty of the paper. It’s easy to imagine that a larger PC would improve reviewing quality by avoiding overload.


Bidding Problems

One way that many conferences in machine learning assign reviewers to papers is via bidding, which has steps something like:

  1. Invite people to review
  2. Accept papers
  3. Reviewers look at title and abstract and state the papers they are interested in reviewing.
  4. Some massaging happens, but reviewers often get approximately the papers they bid for.

At the ICML business meeting, Andrew McCallum suggested getting rid of bidding for papers. A couple reasons were given:

  1. Privacy The title and abstract of the entire set of papers is visible to every participating reviewer. Some authors might be uncomfortable about this for submitted papers. I’m not sympathetic to this reason: the point of submitting a paper to review is to publish it, so the value (if any) of not publishing a part of it a little bit earlier seems limited.
  2. Cliques A bidding system is gameable. If you have 3 buddies and you inform each other of your submissions, you can each bid for your friend’s papers and express a disinterest in others. There are reasonable odds that at least two of your friends (out of 3 reviewers) will get your papers, and with 2 adamantly positive reviews, your paper has good odds of acceptance.

The clique issue is real, but it doesn’t seem like a showstopper to me. If a group of friends succeeds at this game for awhile, but their work is not fundamentally that interesting, then there will be no long term success. The net effect is an unfocused displacement of other perhaps-better papers and ideas.

It’s important to recall that there are good aspects of a bidding system. If reviewers are nonstrategic (like I am), they simply pick the papers that seem the most interesting. Having reviewers review the papers that most interest them isn’t terrible—it means they pay close attention and generally write better reviews than a disinterested reviewer might. In many situations, simply finding reviewers who are willing to do an attentive thorough review is challenging.

However, since ICML I’ve come to believe there is a more serious flaw than any of the above: torpedo reviewing. If a research direction is controversial in the sense that just 2-or-3 out of hundreds of reviewers object to it, those 2 or 3 people can bid for the paper, give it terrible reviews, and prevent publication. Repeated indefinitely, this gives the power to kill off new lines of research to the 2 or 3 most close-minded members of a community, potentially substantially retarding progress for the community as a whole.

A basic question is: “Does torpedo reviewing actually happen?” The evidence I have is only anecdotal, but perhaps the answer is “yes”. As an author, I’ve seen several reviews poor enough that a torpedo reviewer is a plausible explanation. In talking to other people, I know that some folks do a lesser form: they intentionally bid for papers that they want to reject on the theory that rejections are less work than possible acceptances. Even without more substantial evidence (it is hard to gather, after all), it’s clear that the potential for torpedo reviewing is real in a bidding system, and if done well by the reviewers, perhaps even undectectable.

The fundamental issue is: “How do you chose who reviews a paper?” We’ve discussed bidding above, but other approaches have their own advantages and drawbacks. The simplest approach I have right now is “choose diversely”: perhaps a reviewer from bidding, a reviewer from assignment by a PC/SPC/area chair, and another reviewer from assignment by a different PC/SPC/area chair.


Reviewing Horror Stories

Essentially everyone who writes research papers suffers rejections. They always sting immediately, but upon further reflection many of these rejections come to seem reasonable. Maybe the equations had too many typos or maybe the topic just isn’t as important as was originally thought. A few rejections do not come to seem acceptable, and these form the basis of reviewing horror stories, a great material for conversations. I’ve decided to share three of mine, now all safely a bit distant in the past.

  1. Prediction Theory for Classification Tutorial. This is a tutorial about tight sample complexity bounds for classification that I submitted to JMLR. The first decision I heard was a reject which appeared quite unjust to me—for example one of the reviewers appeared to claim that all the content was in standard statistics books. Upon further inquiry, several citations were given, none of which actually covered the content. Later, I was shocked to hear the paper was accepted. Apparently, the paper accidentally went to two different action editors, who each chose distinct reviewers.
  2. Cover Tree. This paper was the first one to give a datastructure for nearest neighbor search for an arbitrary metric which both (a) took logarithmic time under dimensionality constraint and (b) always required space competitive with brute force nearest neighbor search. Previous papers had done (a) or (b), but not both, and achieving both appears key to a practical algorithm, which we backed up with experiments and code.

    The cover tree paper suffered a triple rejection, the last one of which seems particularly poor to me. We submitted the draft to SODA, and got back 3 reviews. The first was blank. The second was a paragraph of positive but otherwise uninformative text. The third was blank. The decision was reject. We were rather confused, so we emailed the program chair asking if the decision was right and if so whether there was any more information we could get. We got back only a form letter providing no further information. Since then, the paper was accepted at ICML.

  3. Ranking Reduction. This paper shows that learning how to predict which of a pair of items is better strongly transfers to optimizing a ranking loss, in contrast to (for example) simply predicting a score and ordering according to predicted score.

    We submitted this paper to NIPS and it had the highest average review of any learning theory paper. The decision was to reject. Based upon what we could make out from a statement by the program committee, the logic of this decision is mostly kindly describable as badly flawed—somehow they confused the algorithm, the problem, and the analysis into a mess. Later it was accepted at COLT. (A bit of disclosure: I was on the program committee at NIPS that year, although obviously not involved in the decision on this paper.)

In all cases where a rejection occurs, the default presumption is that the correct decision was made because most of the time a good (or at least reasonable) decision was made. Consequently, it seems important to point out that there are some objective signs each of the above cases involved poor decisions.

  1. The tutorial paper is fairly widely cited (Google scholar places it 8th amongst my papers), and I continue to find it useful material for a lecture when teaching a class.
  2. The cover tree is also fairly widely cited, and I know from various emails and download counts that it is used by several people. It also won an award from IBM. To this day, it seems odd that an algorithms paper was only publishable at a machine learning conference.
  3. It’s really too soon to tell with the ranking paper, but it was one of the few COLT papers invited to a journal special issue, and there has since been substantial additional work by Mehryar Mohri and Nir Ailon which broadens the claim to other ranking metrics and makes it more computationally tractable.

One of the reasons you hear for why a paper was rejected and then accepted is that the paper improved in the meantime. That’s often true, but in each of the above cases I don’t believe there were any substantial changes between submissions (and for the tutorial it was a perfect accidental experiment).

Normally reviewing horror stories are the academic equivalent of warstories, but these ones have slightly more point. They have each informed my thinking about how reviewing should be done. Relating these stories might make this thinking a bit more understandable.

  1. Reviewer Choice. The tutorial case brings home the impact of how reviewers are chosen. If a paper is to have 3 reviews, it seems like a good idea to choose the reviewers in diverse ways, rather than one way. For example, at a conference, one reviewer by bidding preference, one reviewer by area chair, and one reviewer by another area chair or the program chair’s choice might reduce variance.
  2. Uniform Author feedback. The standard at NIPS was to have author feedback when the ranking paper was submitted. In effect, the standard was not followed for the ranking paper, and it’s easy to imagine this making a substantial difference given how badly flawed the basis of rejection was. It is also easy to imagine that author feedback might have made a difference in the tutorial rejection, as the reviewer was wrong (author feedback was not the standard then).
  3. Decision Basis. It’s helpful to relate the basis of decision by the program committee, especially when it is not summarized in the reviews. The cover tree case was one of the things which led me to add summaries to some of the NIPS papers when I was on the program committee, and I am committed to doing the same for SODA papers I’m reviewing this year. Not having a summary saves the program committee the embarassment of accidentally admitting mistakes, but it is badly disrepectful of the authors and generally promotes misunderstanding.
  4. Fast decisions are bad. It’s not possible to reliably make good decisions about technical matters quickly. I suspect that the time crunch of the NIPS program committee meeting was a contributing factor in the ranking paper case.

As anyone educated in machine learning or statistics understands, drawing 4 conclusions from 3 datapoints is problematic, so the above should be understood as suggestions subject to further evidence.


Motivation should be the Responsibility of the Reviewer

Tags: Machine Learning,Reviewing jl@ 1:48 pm

The prevailing wisdom in machine learning seems to be that motivating a paper is the responsibility of the author. I think this is a harmful view—instead, it’s healthier for the community to regard this as the responsibility of the reviewer.

There are lots of reasons to prefer a reviewer-responsibility approach.

  1. Authors are the most biased possible source of information about the motivation of the paper. Systems which rely upon very biased sources of information are inherently unreliable.
  2. Authors are highly variable in their ability and desire to express motivation for their work. This adds greatly to variance on acceptance of an idea, and it can systematically discriminate or accentuate careers. It’s great if you have a career accentuated by awesome wording choice, but wise decision making by reviewers is important for the field.
  3. The motivation section in a paper doesn’t do anything in some sense—it’s there to get the paper in. Reading the motivation of a paper is of little use in helping the reader solve new problems.
  4. Many motivation sections are a waste of time. The 30th paper on a subject should not require a motivation as if it’s the first paper on a subject, and requiring or expecting this of authors is an exercise in busy work by the research community.

Some caveats to make sure I’m understood:

  1. I’m not advocating the complete removal of a motivation section (motivectomy?), which would be absurd (and frankly harmful to your career). A paragraph describing common examples where the problem addressed comes up is desirable for readers who are not specialists. This paragraph should not be in the abstract, where it seems to often sneak in.
  2. I’m also not arguing against discussion of motivations. I regard discussion of motivations as quite important, and totally unsuited to the paper format. It’s hard to imagine any worse method for discussion than one with a year-size latency where quasi-anonymous people are quasi-randomly paired and each attempts to accomplish several different tasks one of which happens to be a one-sided discussion of motivation. A blog can work much better for this sort of thing, and I definitely invite discussion on motivational questions.

So, how do we change the prevailing wisdom? The answer is always “gradually”, but there are a number of steps we can take.

  1. As an author, one clever technique is to pass serious discussion of motivation by reference. “For a general discussion and motivation of this problem see [].” This would save space in the large number of papers which attempt to address an old problem better than previous approaches.
  2. Participate in public discussion of motivations. We need to encourage a real mechanism for discussion. Until these alternative (and far better) formats for discussion are developed the problem of “who motivates” will always exist.
  3. Have private discussions about motivation where you can. Random conversations at conferences are great for this, and the process often sharpens your appreciation.
  4. Learn to take responsibility for motivation as a reviewer. This might sound hard, but it’s actually somewhat easier than careful evaluation of technical content in my experience.
    1. The first step is to disbelieve all the motivational parts of a paper by default. As mentioned above, the authors are not a reliable source anyways. Skip it and move on.
    2. Make sure you understand the problem being addressed.
    3. Make sure you understand how well the problem is addressed, relative to previous work.
    4. Think about how important that increment is. This is not equivalent to asking “how many people will appreciate the increment?” which is a popularity question. Frankly, all of Machine Learning fails the popularity test in a wider sense, even though many people appreciate the fruits of machine learning on a daily basis. First, think about the problem.
      1. How many people might a solution to the problem help? 0 is fairly common amongst submitted papers.
      2. How much would it help them? If it’s “alot”, then that should add a bit to the importance of the paper.
      3. How familiar are you with the problem? If not very, then it’s appropriate to give the benefit of the doubt to the authors.

      Think about the solution.

      1. This solution might be useful to some other researchers who come up with something useful. This is a a warning sign.
      2. This solution might be useful to me in coming up with a useful algorithm for solving problems.
      3. This paper improves an algorithm. This is also fairly common. It should be improving an algorithm with a reasonable claim at being the best method for solving some problem.
      4. This paper can provide improvements to many algorithms. Theory papers often fall here, but they can also fall under (1) or (2) easily.

      Now, take these considerations into account in forming your own opinion about how motivated the paper is.

  5. Go multimodel. If you only know one model of what machine learning is, you don’t really know machine learning. Learn multiple ideas of what machine learning are, and actively consider their merits and downsides.


Structural Problems in NIPS Decision Making

This is a very difficult post to write, because it is about a perenially touchy subject. Nevertheless, it is an important one which needs to be thought about carefully.

There are a few things which should be understood:

  1. The system is changing and responsive. We-the-authors are we-the-reviewers, we-the-PC, and even we-the-NIPS-board. NIPS has implemented ‘secondary program chairs’, ‘author response’, and ‘double blind reviewing’ in the last few years to help with the decision process, and more changes may happen in the future.
  2. Agreement creates a perception of correctness. When any PC meets and makes a group decision about a paper, there is a strong tendency for the reinforcement inherent in a group decision to create the perception of correctness. For the many people who have been on the NIPS PC it’s reasonable to entertain a healthy skepticism in the face of this reinforcing certainty.
  3. This post is about structural problems. What problems arise because of the structure of the process? The post is not about individual people, because this is unlikely to be fruitful.

Although the subject is nominally about NIPS (which I have experience with as an author, reviewer, and PC member), the points may apply elsewhere.

For those that don’t know, it’s worth reviewing how the NIPS process currently works. Temporally, it looks like the following:

  1. PC chair is appointed.
  2. PC chair picks PC committee to cover many different areas. NIPS is notably diverse.
  3. PC committee members pick reviewers for their areas.
  4. Authors submit blinded papers.
  5. Papers are assigned to two PC committee members, the “primary” and the “secondary”.
  6. Reviewers bid for papers within their areas which they want and don’t want to review.
  7. Reviewers are assigned papers based on bid plus coverage.
  8. Reviewers review papers.
  9. Authors respond to blinded reviews.
  10. Reviewers discuss and rate papers.
  11. PC members digest author/reviewer interaction (and sometimes the paper) into an impression.
  12. PC members meet physically at the PC meeting.
  13. PC members present all papers that they believe are worth considering to other PC members and a decision is made.

Naturally, there are many details left out of this long list.

Here is my attempt to describe the problems I’ve seen:

  1. Attention deficit disorder. The attention paid to individual accept/reject decisions is (and structurally must be) small. There are several effects which drive this:
    1. The people on the NIPS PC are typically busy and time constrained.
    2. The number of papers assigned to individual PC members is large—perhaps 40 to 80, plus a similar number assigned as a secondary.
    3. Many of the people have traveled a very long ways to reach the PC meeting. Jetlag is common, and often significantly effects your ability to think carefully.
    4. The meeting itself is 2 days long. The average time spent on any decision must be less than 5 minutes, and everyone knows this. The implicit encouragement to digest a paper down to its most simple description is significant. No one on the PC has seen the paper except for the primary and the secondary (if you are lucky) PC members, so decisions are made quickly based upon relatively little information. (This is better than it sounds in most cases because effectively the decision was made by the primary PC member beforehand.)
  2. Artificial scarcity. NIPS is a single track conference with 3 levels of acceptance “Accept for an oral presentation”, “Accept for a poster with a spotlight”, and “Accept as a poster only”. It’s fairly difficult to justify a paper as “of broad interest”, which is ideal for an oral presentation. Will a neuroscientist really pay attention to this learning theory paper? Is this dimensionality reduction algorithm going to interest someone in learning theory? It’s substantially easier to justify a paper as “possibly of interest to a number of people”, which is about right for poster spotlight. Since the number of spotlights and the number of orals is similar, two effects occur: papers which are about right for spotlights become orals, and many reasonable spotlights aren’t spotlights because they don’t fit.
  3. The Veto Effect. If someone on the PC has a strong dislike for your paper, there is a very good chance for reject. This is true even when attention is explicitly payed by the PC chair to avoiding the veto problem. It’s even true when your paper has the strongest reviews in the area (no joke!). There are several fundamental problems here:
    1. People, especially in person, do not generally want to be confrontational. Consequently, if someone who is rarely confrontational speaks strongly against a paper, it’s rare2 for an alternate voice to be heard.
    2. It is easy to instill “fear, uncertainty, and doubt” in people. Was this paper covering the same material as some other paper no one knows? Are the assumptions criticizable? This problem is greatly exaggerated by attention deficit disorder.

It is easy to complain about these problems and substantially harder to fix them. (There is previous discussion on this.) Here is my best attempt to imagine fixes.

  1. Attention Deficit Disorder. The fundamental problem here is that papers aren’t getting the attention that they deserve by the final decision maker. Several changes might help, but nothing is going to be a silver bullet here.
    1. Author responsibility. Unfortunately, some authors abuse the system by submitting papers which should not be submitted. Much of this has to do with inexperience—many authors are first time paper writers. For these authors, some better effort educating people about what is an appropriate paper is good. This year, an effort was made to do this, and followups may be helpful. For a small fraction of papers, authors intentionally skate the edge of what is reasonable. Should an ICML paper with 30% different content be submitted to NIPS? This small fraction takes more time than their fraction indicates and (frankly) isn’t always caught. Some form of “shame list” may be an appropriate way to deal with this, although much caution would have to be exercised.
    2. Many of the problems here are unremovable artifacts of a physically present PC meeting. Going to a virtualized process would eliminate these problems (and introduce others). Any such decision would have to be carefully considered, but it is not impossible—there are plenty of succesful conference committees which never meet physically.
    3. The PC meeting can be run a bit differently.
      1. Bob Williamson and I managed to go through our secondary assignments and make independent decisions, then reconcile. In contrast, for most papers, the secondary PC member was inoperative at the PC meeting. This made some difference, and it’s easy to imagine that systematically having this reconciliation be a part of the PC meeting is helpful. The reconciliation step does not take very long and is parallelizable.
      2. Not making a decision at the PC meeting could be a real option for a small number of troublesome papers. There is perhaps a week-long timegap between the PC meeting and the release of the decisions during which decisions could be double checked. This option must only be used rarely, and never as a means for excluding interested PC members from the decision.
      3. Information can be more widely shared. I don’t see any real advantage to limiting the knowledge of papers not in your area to “title+authors”. At the PC meeting itself, it would be helpful to have all of the papers available to all of the members.
  2. Artificial Scarcity. My understanding is that the makers of NIPS purposefully preferred a single track conference, and it’s hard to argue with the success NIPS has enjoyed. Nevertheless, it seems notable that the NIPS workshops (which are excessively multitracked) are more succesful than the NIPS conference by some measures. Going to a two-track or partially two-track format would ease some of the decision making.

    Even working within the single track format, it’s not clear that the ratio between orals and spotlights is right. Spotlights take about 1/10th the time that an oral presentation takes, and yet only 1/10th or so of the overall time is allocated to spotlight presentations. Losing one oral presentation (out of about 20) would yield a
    significant increase in the number of spotlights, and it’s easy to imagine this would be beneficial to attendees while easing decision making.

  3. The Veto Effect. The veto effect is hard to deal with, and it’s only relevant to a small number of decisions. Nevertheless it’s important because some of the best papers are controversial at the time they are published. The are two ways I can imagine for dealing with the veto effect: (1) allowing author feedback (2) devolving power from the PC to the reviewers. Allowing author feedback would have to be coupled with delayed decision making. Eliminating the power of the PC to reject very highly rated papers is also controversial, but may be worth considering.


Health of Conferences Wiki

Aaron Hertzmann points out the health of conferences wiki, which has a great deal of information about how many different conferences function.


Incentive Compatible Reviewing

Tags: Papers,Research,Reviewing jl@ 10:13 pm

Reviewing is a fairly formal process which is integral to the way academia is run. Given this integral nature, the quality of reviewing is often frustrating. I’ve seen plenty of examples of false statements, misbeliefs, reading what isn’t written, etc…, and I’m sure many other people have as well.

Recently, mechanisms like double blind review and author feedback have been introduced to try to make the process more fair and accurate in many machine learning (and related) conferences. My personal experience is that these mechanisms help, especially the author feedback. Nevertheless, some problems remain.

The game theory take on reviewing is that the incentive for truthful reviewing isn’t there. Since reviewers are also authors, there are sometimes perverse incentives created and acted upon. (Incidentially, these incentives can be both positive and negative.)

Setting up a truthful reviewing system is tricky because their is no final reference truth available in any acceptable (say: subyear) timespan. There are several ways we could try to get around this.

  1. We could try to engineer new mechanisms for finding a reference truth into a conference and then use a ‘proper scoring rule’ which is incentive compatible. For example, we could have a survey where conference participants short list the papers which interested them. There are significant problems here:
    1. Conference presentations mostly function as announcements of results. Consequently, the understanding of the paper at the conference is not nearly as deep as, say, after reading through it carefully in a reading group.
    2. This is inherently useless for judging reviews of rejected papers and it is highly biased for judging reviews of papers presented in two different formats (say, a poster versus an oral presentation).
  2. We could ignore the time issue and try to measure reviewer performance based upon (say) long term citation count. Aside from the bias problems above, there is also a huge problem associated with turnover. Who the reviewers are and how an individual reviewer reviews may change drastically in just a 5 year timespan. A system which can provide track records for only a small subset of current reviewers isn’t very capable.
  3. We could try to manufacture an incentive compatible system even when the truth is never known. This paper by Nolan Miller, Paul Resnick, and Richard Zeckhauser discusses the feasibility of this approach. Essentially, the scheme works by rewarding reviewer i according to a proper scoring rule applied to P(reviewer j’s score | reviewer i’s score). (A simple example of a proper scoring rule is log[P()].) This is approach is pretty fresh, so there are lots of problems, some of which may or may not be fundamental difficulties for application in practice. The significant problem I see is that this mechanism may reward joint agreement instead of a good contribution towards good joint decision making.

None of these mechanisms are perfect, but they may each yield a little bit of information about what was or was not a good decision over time. Combining these sources of information to create some reviewer judgement system may yield another small improvement in the reviewing process.

The important thing to remember is that we are the reviewers as well as the authors. Are we interested in tracking our reviewing performance over time in order to make better judgements? Such tracking often happens on an anecdotal or personal basis, but shifting to an automated incentive compatible system would be a big change in scope.


NIPS paper evaluation criteria

John Platt, who is PC-chair for NIPS 2006 has organized a NIPS paper evaluation criteria document with input from the program committee and others.

The document contains specific advice about what is appropriate for the various subareas within NIPS. It may be very helpful, because the standards of evaluation for papers varies significantly.

This is a bit of an experiment: the hope is that by carefully thinking about and stating what is important, authors can better understand whether and where their work fits.

Update: The general submission page and Author instruction including how to submit an appendix.


Reviewing techniques for conferences

Tags: Reviewing jl@ 9:28 pm

The many reviews following the many paper deadlines are just about over. AAAI and ICML in particular were experimenting with several reviewing techniques.

  1. Double Blind: AAAI and ICML were both double blind this year. It seemed (overall) beneficial, but two problems arose.
    1. For theoretical papers, with a lot to say, authors often leave out the proofs. This is very hard to cope with under a double blind review because (1) you can not trust the authors got the proof right but (2) a blanket “reject” hits many probably-good papers. Perhaps authors should more strongly favor proof-complete papers sent to double blind conferences.
    2. On the author side, double blind reviewing is actually somewhat disruptive to research. In particular, it discourages the author from talking about the subject, which is one of the mechanisms of research. This is not a great drawback, but it is one not previously appreciated.
  2. Author feedback: AAAI and ICML did author feedback this year. It seemed helpful for several papers. The ICML-style author feedback (more space, no requirement of attacking the review to respond), appeared somewhat more helpful and natural. It seems ok to pass a compliment from author to reviewer.
  3. Discussion Periods: AAAI seemed more natural than ICML with respect to discussion periods. For ICML, there were “dead times” when reviews were submitted but discussions amongst reviewers were not encouraged. This has the drawback of letting people forget their review before discussing it.


Grounds for Rejection

Tags: Reviewing jl@ 6:31 pm

It’s reviewing season right now, so I thought I would list (at a high level) the sorts of problems which I see in papers. Hopefully, this will help us all write better papers.

The following flaws are fatal to any paper:

  1. Incorrect theorem or lemma statements A typo might be “ok”, if it can be understood. Any theorem or lemma which indicates an incorrect understanding of reality must be rejected. Not doing so would severely harm the integrity of the conference. A paper rejected for this reason must be fixed.
  2. Lack of Understanding If a paper is understood by none of the (typically 3) reviewers then it must be rejected for the same reason. This is more controversial than it sounds because there are some people who maximize paper complexity in the hope of impressing the reviewer. The tactic sometimes succeeds with some reviewers (but not with me).

    As a reviewer, I sometimes get lost for stupid reasons. This is why an anonymized communication channel with the author can be very helpful.

  3. Bad idea Rarely, a paper comes along with an obviously bad idea. These also must be rejected for the integrity of science

The following flaws have a strong negative impact on my opinion of the paper.

  1. Kneecapping the Giants. “Kneecapping the giants” papers take a previously published idea, cripple it, and then come up with an improvement on the crippled version. This often looks great experimentally, but is unconvincing because it does not improve on the state of the art.
  2. Only Toys. The paper emphasizes experimental evidence on datasets specially created to show the good performance of their algorithm. Unfortunately, because learning is worst-case-impossible, I have little trust that performing well on a toy dataset implies good performance on real-world datasets.

My actual standard for reviewing is quite low, and I’m happy to approve of incremental improvements. Unfortunately, even that standard is such that I suggest rejection on most reviewed papers.

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