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Peer Review

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This blog is not peer reviewed at all.  I write it, I put it out there, and people read it or not. It is my little megaphone that I alone control.

But I don’t think anyone, or at least I hope that no-one, thinks that I am publishing scientific papers here.  They are my opinion pieces, and only worthwhile if there are people who have found my previous opinions to have turned out to be right in some way.

There has been a lot of discussion recently about peer review. This post is to share some of my experiences with peer review, both as an author and as an editor, from three decades ago.

In my opinion peer review is far from perfect. But with determination new and revolutionary ideas can get through the peer review process, though it may take some years. The problem is, of course, that most revolutionary ideas are wrong, so peer review tends to stomp hard on all of them. The alternative is to have everyone self publish and that is what is happening with the arXiv distribution service. Papers are getting posted there with no intent of ever undergoing peer review, and so they are effectively getting published with no review. This can be seen as part of the problem of populism where all self proclaimed experts are listened to with equal authority, and so there is no longer any expertise.

My Experience with Peer Review as an Author

I have been struggling with a discomfort about where the herd has been headed in both Artificial Intelligence (AI) and neuroscience since the summer of 1984. This was a time between my first faculty job at Stanford and my long term faculty position at MIT. I am still concerned and I am busy writing a longish technical book on the subject–publishing something as a book gets around the need for full peer review, by the way…

When I got to MIT in the fall of 1984 I shifted my research based on my concerns. A year later I was ready to talk about the what I was doing, and submitted a journal paper describing the technical idea and an initial implementation. Here is one of the two reviews.

It was encouraging, but both it and a second review recommended that the paper not be published. That would have been my first rejection.  However, the editor, George Bekey, decided to publish it anyway, and it appeared as:

Brooks, R. A. “A Robust Layered Control System for a Mobile Robot, IEEE Journal of Robotics and Automation, Vol. 2, No. 1, March 1986, pp. 14–23; also MIT AI Memo 864, September 1985.

Google Scholar reports just under 12,000 citations of this paper, my most cited paper ever. The approach to controlling robots, the subsumption architecture that it proposed led directly to the Roomba, a robot vacuum cleaner, which with over 30 million sold is the most produced robot ever. Furthermore the control architecture was formalized over the years by a series of researchers, and its descendant, behavior trees, is now the basis for most video games. (Both Unity and Unreal use behavior trees to specify behavior.) The paper still has multi billion dollar impact every year.

Most researchers who stray, believing the herd is wrong, end up heading off in their own wrong direction. I was extraordinarily lucky to choose a direction that has had incredible practical impact.

However, I was worried at a deeper intellectual level, and so almost simultaneously started writing about the philosophical underpinnings of research in AI, and how my approach differed. There the reviews were more brutal, as is shown in a review here:

This was a a review of lab memo AIM-899, Achieving Artificial Intelligence through Building Robots which I had submitted to a conference.This paper was the first place that I talked about the possibility of robot vacuum cleaners as an example of how the philosophical approach I was advocating could lead to new practical results.

The review may be a little hard to read in the image above. It says:

This paper is an extended, wandering complaint that the world does not view the author’s work as the salvation of mankind.

There is no scientific content here; little in the way of reasoned argument, as opposed to petulant assertions and non-sequiturs; and ample evidence of ignorance of the literature on these questions. The only philosopher cited is Dreyfus–but many of the issues raised have been treated more intelligibly by others (the chair definition problem etc. by Wittgenstein and many successors; the interpreted toy proscription by Searle; the modularity question by Fodor; the multiple behaviors ideas by Tinbergen; and the constructivist approach by Glymour (who calls it computational positivism). The argument about evolution leaks all over, and the discussion on abstraction indicates the author has little understand of analytic thought and scientific investigation.

Ouch! This was like waving a red flag at a bull. I posted this and other negative reviews on my office door where they stayed for many years. By June of the next year I had added to it substantially, and removed the vacuum cleaner idea, but kept in all the things that the reviewer did not like, and provocatively retitled it Intelligence Without Representation. I submitted the paper to journals and got further rejections–more posts for my door. Eventually its fame had spread to the point that the Artificial Intelligence Journal, the mainstream journal of the field, published it unchanged (Artificial Intelligence Journal (47), 1991, pp. 139–159) and it now has 6,900 citations. I outlasted the criticism and got published.

That same year at the major international conference IJCAI: International Joint Conference on Artificial Intelligence I was honored to win the Computers and Thought award, quite a surprise to me, and I think to just about every one else. With that honor came an invitation to have a paper in the proceedings without the six page limit that applied to everyone else, and without the peer review process that applied to everyone else. My article was twenty seven pages long, double column, a critical review article of the history of AI, also with a provocative and complementary title, Intelligence Without Reason, (Proceedings of 12th Int. Joint Conf. on Artificial Intelligence, Sydney, Australia, August 1991, pp. 569–595). It now has over 3,100 citations.

My three most cited papers were either rejected under peer review or accepted with no peer review.  So I am not exactly a poster child for peer reviewed papers.

My Experience With Peer Review As an Editor

In 1987 I co-founded a journal, the International Journal of Computer Vision. It was published by Kluwer as a hardcopy journal for many years, but now it is run by Springer and is totally online. It is now in its 128th volume, and has had many hundreds of issues. I co-edited the first seven volumes which together had a total of twenty eight issues.

The journal has a very strong reputation and consistently ranks in the top handful of places to publish in computer vision, itself a very hot topic of research today.

As an editor I soon learned a lot of things.

  1. If a paper was purely theoretical with lots of equations and no experiments involving processing an image it was much more likely to get accepted than a paper which did have experimental results. I attributed this to people being unduly impressed by mathematics (I had a degree in pure mathematics and was not as easily impressed by equations and complex notation). I suspected that many times the reviewers did not fully read and understand the mathematics as many of them had very few comments about the contents of such papers. If, however, a paper had experiments with real images (and back then computers were so slow it was rarely more than a handful of images that had been processed), the same reviewers would pick apart the output, faulting it for not being as good as they thought it should be.
  2. I soon learned that one particular reviewer would always read the mathematics in detail, and would always find things to critique about the more mathematical papers. This seemed good. Real peer review. But soon I realized that he would always recommend rejection. No paper was ever up to his standard. Reject! There were other frequent rejecters, but none as dogmatic as this particular one.
  3. Likewise I found certain reviewers would always say accept. Now it was just a matter of me picking the right three referees for almost any paper and I could know whether the majority of reviewers would recommend acceptance or rejection before I had even sent the paper off to be reviewed. Not so good.
  4. I came to realize that the editor’s job was real, and it required me to deeply understand the topic of the paper, and the biases of the reviewers, and not to treat the referees as having the right to determine the fate of the paper themselves. As an editor I had to add judgement to the process at many steps along the way, and to strive for the process to improve the papers, but also to let in ideas that were new. I now came to understand George Bekey and his role in my paper from just a couple of years before.

Peer reviewing and editing is a lot more like the process of one on one teaching than it is of processing the results of a multiple choice exam. When done right it is about coaxing the best out of scientists, and encouraging new ideas to flourish and the field to proceed.


Those who think that peer review is inherently fair and accurate are wrong. Those who think that peer review necessarily suppresses their brilliant new ideas are wrong. It is much more than those two simple opposing tendencies.

Peer review grew up in a world where there were many fewer people engaging in science than today. Typically an editor would know everyone in the world who had contributed to the field in the past, and would have enough time to understand the ideas of each new entrant to the field as they started to submit papers. It relied on personal connections and deep and thoughtful understanding.

That has changed just due to the scale of the scientific endeavor today, and is no longer possible in that form.

There is a clamor for double blind anonymous review, in the belief that that produces a level playing field. While in some sense that is true, it also reduces the capacity for the nurturing of new ideas. Clamorers need to be careful what they wish for–metaphorically it reduces them to competing in a speed trial, rather than being appreciated for virtuosity. What they get in return for zeroing the risk of being rejected on the basis of their past history or which institution they are from is that they are condemned to forever aiming their papers at the middle of a field of mediocrity, with little chance for achieving greatness.

Another factor is that the number of new journals has changed. Institutions, and sometimes whole countries, decide that the way for them to get a better name for themselves is to have a scientific journal, or thirty. They set them up and put one of their local people who has no real understanding of the flow of ideas in the particular field at the global scale, as editor. Now editing becomes a mechanical process, with no understanding of the content of the paper or the qualifications of who they ask to do the reviews. I know this to be true as I regularly get asked to review papers in fields in which I have absolutely no knowledge, by journal editors that I have never heard of, nor of their journal, nor its history. I have been invited to submit a review that can not possibly be a good review. I must induce that other reviews may also not be very good.

I don’t have a solution, but I hope my observations here might be interesting to some.

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