• Research results are more important than the number of publications or citations.
  This is fine. Yet, we don’t have time to read your papers. So, just keep publishing a lot of papers each year. And get your influential friends to cite you. That’s how we’ll know whether you are good.
• Science and truth are more important than spin and marketing.
  Yes, but keep pretending you will solve world hunger. And align your research results with the current fashionable trends.
• You cannot tell where the next science breakthrough is going to come from.
  Maybe. Still, we want a plan of your research activities for the next five years.

Further reading: The hard truth about research grants and The secret behind radical innovation.

Source : Manifesto for Half-Arsed Agile Software Development via John D. Cook.

• Permanent researchers publish more when they are in smaller labs.
• Having many Ph.D. students fails to improve productivity.
• Funding has little effect on research productivity.

Reference: Carayol, N. and Matt, M., Individual and collective determinants of academic scientists’ productivity, Information Economics and Policy 18 (1), 2006.

Further reading (on this blog): To be smarter, ignore external rewards, Is collaboration correlated with productivity?, Big schools are no longer giving researchers an edge?

Deolalikar claims to have solved the famous P versus NP problem. Is the proof correct? Some influential researchers doubt it: Scott Aaronson is betting 200k$ of his own money against Deolalikar.

What I find most interesting is that Deolalikar did not submit the paper to a journal, as far as I know. He didn’t even post it on arxiv like Perelman. Yet, he is receiving much attention. His name is being tweeted several times a minute. Many of the most influential theoretical computer scientists are reacting to the paper. He is getting the best peer review possible. Most similar papers don’t get so much attention.

Why is this paper different?

• Everyone seems to agree that the paper is well written, it has nice (color!) figures and the reference section appears up-to-date and complete.  If your result is important, communicate it well.
• Deolalikar has published just a handful of papers in theoretical computer science, and none at the major conferences. But he has enough peer-reviewed research papers to be treated as a peer.
• While I doubt he was hired to work on complexity theory, Deolalikar is an industry researcher at HP. Being paid to do research might make you more credible.

Further reading: Deolalikar’s publication list on DBLP, A Proof That P Is Not Equal To NP? by Lipton and P ≠ NP by Baker.

Update: Porreca has the best write-up on reactions to this paper.

Update 2: The consensus after two weeks is that the proof wrong and unfixable.

I often come across the following type of arguments in research papers:

• You could save 3 bits of storage for every value in your database. Surely that’s irrelevant. Nobody cares about saving 3 bits!
• You can sort arrays in 10 ms. Surely, that cannot be improved upon? You are already down to 10 ms and nobody cares about such small delays.

I hope you can see what is wrong with these statements?

I call it the fallacy of absolute numbers: you express a measure or a gain in absolute value, and then conclude to optimality or near optimality because the number appears small (or large).

Remember: Saving 3 bits of storage out of 6 bits is a 2:1 compression ratio. Sorting in 5 ms instead of 10 ms doubles the speed.

Disclaimer: I am sure that someone else has documented this fallacy, but I could not find any reference to it.

A common advice given out to young researchers is to find a niche. (See Michael’s Branding Your Research). That is certainly good advice. Instead of being another young researcher, you can be the new guy working on topic X. But it always seems to happen no matter what: most Ph.D. thesis address a narrow topic. I believe that the real advice people would like to give is: find yourself a nice topic, and make sure this topic becomes fashionable. Of course, this implies that you can somehow predict the future, or have a thesis supervisor with enough clout that he can either initiate new trends, or have inside knowledge regarding the upcoming trends.

A more interesting question is what you should do with the rest of your career, assuming you landed a research job, somehow. Should you find yourself one or two niche topics and stay there for the rest of your life? That is a common strategy. You save precious time: instead of having to skim 100 research articles a year, you may get by with 20 or 30 research articles, or even less. Moreover, because you are the leading authority on one or two topics, you can never be caught unaware. You never have to worry about finding new topics: you just keep on iteratively improving whatever you are doing right now. With some luck, you can reuse your funding proposals year after year. Finally, you can quickly get to know everyone that matters regarding these narrow topics. And that is a perfectly good strategy.

The problems begin when we associate the lack of a steady trajectory with failure. Encouraging static research topics leads to conservatism. Meanwhile, some of the most innovative researchers have cultivated varied interests. Von Neumann was a set theorist, but he wrote 20 papers in Physics, and even in Mathematics, he covered a wide range of topics (set theory, logic, topological groups, measure theory, ergodic theory, operator theory, and continuous geometry). Would we have been better off had von Neumann remained a pure set theorist?

And I tend to have more trust in researchers who have their eggs in different baskets. They can afford to be a bit more critical.

Warning: I am not urging Ph.D. students to change topic repeatedly while writing up their thesis. Finish whatever you start. And be aware that approaching a new research topic can be costly.

Technological progress tends to increase the available information. Thus, our capacity to manage this information becomes overloaded (hence the term information overload). As Clay Shirky explained: it is not so much an information overload, as a filter failure. The abundance of information is never a problem. The real problem is the lack of efficient strategies to index, summarize, filter, cross-reference and archive information.

But information overload is nothing new. In Reading Strategies for Coping With Information Overload ca. 1550-1700, Blair surveys the techniques our ancestors invented to cope with the abundance of books :

• the alphabetical index;
• the reference book,
• copy and paste (with actual scissors) to save time in note-taking.

What I find fascinating is the historical perspective: while still useful, the alphabetical index is hardly exciting anymore. It has been supplanted by full text search (in e-books). There are still reference books (such as dictionaries), but they are being replaced with online tools. Information overload continues to generate many inventions: the search engine (such as Google), the recommender system (as on Amazon.com), and the social networks (such as Twitter). Literally, these tools expand our minds. We become smarter.

Yet, every time I finish writing a research article, I am amazed at how old fashioned the format is.

• Research journals still ask for silly metadata such as keywords, even though most researchers rely on full text search.
• The format is clearly meant for paper, even though most of my collaborators browse research articles on their computers.
• We have silly things like page limitations.
• It is excessively difficult to correct or improve a “published” article.

There is hope. The PLoS One journal presents research articles in an innovative format. The article is interactive: anyone can rate and comment it. Many journals allow the authors to upload supplementary material. Yet, I predict that in 20 years, we will look back and think that academic publishing in 2010 was archaic. (I admit that it is not a daring prediction.) There is much room for innovation.

Source: Erik Duval.

The greatest challenge for a researcher is to choose projects that have a good chance of delivering impact. Alain Désilets from NRC—co-author of VoiceGrip, Webitext and the Cross Lingual Wiki Engine—shared his strategies with me:

• Look at how many workdays per week you can dedicate to research and make that be the number of projects you can work on in parallel. In other words, if you are one of the lucky few who can dedicate 5 days per week doing research, then you have room for 5 projects.
• Invest your energy proportionally to the amount of positive feedback you receive for each project. This includes collaboration offers, grants, potential users, and so on.
• Never work alone on a project for too long. It’s OK to start exploring a compelling idea on your own for a couple of months, but if you can’t convince someone else to work with you on it, maybe it’s not such a great idea after all. Maybe it’s technically infeasible, maybe there is no need or market for it, or maybe it’s just too much ahead of its time. Don’t completely give up on the idea yet. Put it on the ice for now and keep sharing that idea with people until you meet the right people to make it happen with you.
• Instead of looking for partnership money which will require you to spend months drafting and revising agreements (who wants to deal with lawyers anyway), look for talented people who have control over their own time, and are willing to invest some of that precious resource working with you on an idea. Don’t worry about who will own the baby before it’s actually born (that usually ensures that the work relationship will never get off the ground). Just make sure everyone keeps a lab book documenting who did what so that you will have a basis to argue in a friendly and civilised manner about who owns what share of the baby, if you ever have that nice problem.
• Talk to lots of different people from different walks of life about your idea. You never know who will give you the insight or contact you need to advance to the next level on a given project. Of course if you do this, you pretty much give up on the idea of patenting your idea.
• Make sure you collocate in time and space as much as you can with your collaborators. There was a time when I had 5 projects (those were the happy days of 5 days of research per week), and I had scheduled things so that on Mondays I would work with Joe on project X, Tuesdays were dedicated to working on project Y with Jane, and so on.
• Find and organisation or a type of end users with an interesting problem that you think you could solve using some bleeding edge technology. Become very intimate with the problem, maybe even pretending to do these people’s job for a day. Once you understand their problem well, don’t jump right away to the hi-tech solution. Instead, start with the Simplest Thing That Could Possibly Work, and only add complex technology where and when it is needed. This may not get you a publication in a first tier journal, but it greatly increases your odds of developing a system that will actually be used. Plus, when you DO find that you need sophisticated technology, you know exactly why, and what the actual value added is.
• Use Agile Development practices which allow you to advance your projects in short, highly focused bursts of a few days (1-day burst are even possible). Write lots of short “stories” that describe things you can accomplish in a day or less, and keep re-prioritizing them so that the ones that currently add the most value to your target users are always at the top. Use Test Driven Development to ensure that your system is always stable and that you can put it aside for a few days or months, yet pick up right from where you left. These kinds of techniques are essential if you want to be able to quickly reallocate your effort depending on how hot your different projects are.

Disclaimer: it does not necessarily  reflect the views of his employer.

The publishing house Elsevier invited me to fill out a survey regarding their journals. As a reward, they gave me a glimpse at their statistics.

The three most important considerations when choosing a research journals are (in order) :

1. Speed of review process
2. Standard of reviews
3. Overall reputation of the journal

And the activity researchers complained to most about? Peer reviewing manuscripts.

In any case, if you want to build a good journal and attract great papers, make sure you have fast and competent peer review. (Duh!) Meanwhile, having a good printer or a good editorial board are much less important.

Zed A. Shaw—author of several books on Ruby and Python—came up with an interesting criticism of Computer Science. He makes some good points:

Computer Science is a pointless discipline with no culture. (…) They rarely teach deep philosophy and instead would rather either teach you what some business down the street wants, or teach you their favorite pet language like LISP. (…) Another way to explain the shallowness of Computer Science is that it’s the only discipline that eschews paradox. Even mathematics has reams of unanswered questions and potential paradox in its core philosophy. (…) There’s an envelope of knowledge so vast in most other disciplines that just when you think you’ve learned it all you find something else you never knew. This is what makes them interesting.

Oh! I think there are many deep and exciting questions in Computer Science. (And not just whether P is equal to NP.) And do Sociology, Economics and History have more depth? But I agree that Computer Science is too often utilitarian. Some like to pretend that by catering to the perceived needs of industry, graduates will get better jobs. Unfortunately, too often, the students have to unlearn their so-called “practical knowledge” once they leave the campus. The honest truth: you don’t need three or four years of college to do great in the software industry.

Maybe more time should be spent on the deep questions. Here are a few discussion points that come to mind :

• What is “meaning” and how can computation capture or codify it? What does it say about our brain? Is our brain a Turing machine?
• Why are some programmers ten times more productive than others?
• Can computers extend our intelligence? How intelligent can we become?

Funding agencies in Canada seek to emulate American funding agencies by promoting excellence. What this means in concrete terms is that few professors get most of the resources whereas the bulk of University professors are left with a pitance or nothing. The intuition behind this more competitive approach is that we must catch up with the American efficiency. We must reward the most productive researchers and stop wasting money with the unproductive ones. (Disclaimer: I am happy with the research grants I got so far. Luckily, I have been judged to be productive…)

But how is the American system holding out against the competition? I looked at the countries publishing most research papers in Computer sciences, in 1998 and then in 2008.

1998:

1. USA (14,294 papers)
2. Japan (2,941 papers)
3. United Kingdom (2,706 papers)

2008:

1. USA (15,744 papers)
2. China (14,680 papers)
3. United Kingdom (5,703 papers)

It appears that whereas most countries have doubled or more their production of research papers, the USA has stood still. Because these numbers are for 2008, I conjecture that right now, in 2010, Chinese researchers already publish more than their American counterparts. Of course, American authors are more cited, but the gap between China and the USA is closing in this respect as well. Interestingly, Americans also appear to be losing their edge compared to the  United Kingdom, France, Germany and Canada.

While I do not have enough evidence to conclude, I conjecture that an all-or-nothing approach, so common in the USA, may not be so efficient after all. By leaving most University professors behind, you are wasting precious resources. And I fear that by emulating this model, Canada might be losing out too.

Source: SJR.