The Importance of Auditing Your Work Habits

An Autumn Audit

I had to travel unexpectedly last weekend, so I missed my normal household chores. This morning, I woke up to the lawn picture above. Because I don’t have class or meetings scheduled today (a miracle!), I decided to take an hour or so to clean things up.

I never mind working outside, as it has the nice effect of moving my thoughts beyond the immediate future, and allowing me to perform a bigger picture audit of where things stand in my life. Today, I was thinking a lot about my work habits.

By the time I had the lawn looking like this…

…I had wrapped up some nice epiphanies.

Standing on Shoulders in Search of Important Problems

As I worked, my mind wandered to earlier this week, when I hosted a visiting scholar at Georgetown. He had recently published a nice result.

Some quick background: there is a network-related algorithm problem — how quickly can you schedule a connected structure in a wireless network with additive interferencethat was introduced in 2006, and has received steady attention since. The first known solution required time relative to the logarithm of the network size raised to the fourth power, but this was quickly knocked down to cubic and then quadratic, where it has stalled since 2007. That is, until earlier this year, when my visitor, working with his collaborator, dropped the result down to the straight logarithm, which is almost certainly the best you can do.

This is an example of what I call an important result, because there’s a community of researchers who immediately recognized its value (in this case, because it improved a bound that lots of people had been trying, and failing, to improve). For an applied mathematician, important results are the bread and butter of a successful academic career.

Naturally, I asked the visitor about how he came to his big finding.

The short answer was reading. He had been trying to understand another important result in his field, which had been published the year before, and in doing so stumbled onto a technique that allowed his breakthrough.

This knowledge-driven approach to breakthroughs should sound familiar, as it turned up again and again in my previous study of the impact instinct. I also detail the phenomenon in Rule 4 of SO GOOD. To summarize: new important results almost always require expert-level knowledge of existing important results.

The implication is that, as an academic, I should be spending a significant portion of my time reading and trying to understand the best work in my field. As I raked and mowed this morning, I performed an internal audit, and came to the conclusion that although I do this,  I’m not doing it nearly enough if I want to make a big splash.

My Skewed Project Ratio

Here’s the problem that’s keeping me from more time diving into the existing literature in search of important problems…

I currently have 10 projects that I consider active (i.e., they receive regular attention). Only 2 of these projects are aimed at improving results that are well-known in the existing literature. The other 8 are speculative, by which I mean my collaborators and I essentially invented them.

To be clear, there’s nothing intrinsically wrong with speculative projects, especially when you’re combining disciplines (which almost always requires new problems to be identified). But they take time to maintain, are prone to fizzling (when you invent a problem there’s always a good chance that it will end up either trivial or impossible), and because they’re new, you tend to get less recognition for them once published. Eight such projects is too many.

A better mix for me would be 2 – 3 literature-driven projects and perhaps no more than 2 speculative projects at a time. The reduced load would allow me to advance results faster, so I wouldn’t expect my overall rate of publishing to reduce. But it would also skew my output so that at least half of my papers are geared toward potential important results. This is a much better ratio for a pre-tenure theoretician.

There’s no mystery as to how I fell into my current unequal balance: speculative projects are easy to start, while literature-driven projects can be difficult to find and always require lots of struggling with hard papers .

Which is why I’m glad I performed an audit this morning: If I had relied on the behaviors that were appealing in the short term, I would have continued to sell short my long term success.


The above details on how one produces important applied mathematics results are unlikely to be relevant to your career. But the bigger picture conclusion here is relevant: we should all regularly perform audits where we ask ourselves how we are currently spending our work time and how we should be spending this time. This sounds like a basic idea, but few of us actually do it. The lesson I’ve learned is that the best practices for a specific job are not always obvious without reflection. Furthermore, you can’t trust your instincts to lead your day-to-day decisions toward the best outcomes. Craftsmanship, in other words, requires guidance.


This post is part of my Craftsman in the Cubicle series which explores strategies for building a remarkable working life by mastering a small number of rare and valuable skills. Previous posts include:


26 thoughts on “The Importance of Auditing Your Work Habits”

  1. What a timely article! I love it when two of my favorite bloggers coincide in a topic. Bertrand Meyer recently blogged about how trends in research *funding* are running counter to the goals of ‘read existing research and improve existing results.’ Meyer argues that this funding trend is dangerous. Your anecdotes here today, Cal, help further illustrate how such a funding trend is misguided. The conclusions of your specific personal audit show that you would benefit from spending additional time reading deeply about existing important results, and that you should increase the proportion of your projects that focus on improving results that are well-known in the existing literature. However, Meyer shows that funding entities might not agree with you. How tragic!

  2. I meant to provide a link to the Meyer viewpoint, aptly titled “Long Live Incremental Research!

    Ah, I read that article! Fortunately, in more mathematical fields, this problem is not so pronounced. Improving/solving well-established hard problems gathers easy funding. In the biological sciences, however, the funding seems more aimed toward bold new ideas, as Meyer’s discusses.

  3. Great article. However, I have a question: You suggest reading many articles in your field to get new ideas. On the other hand, the director of my PhD programm (Mathematics) recently said that our greatest asset as early-career researchers is our ignorance and that the worst mistake we could make is to go to the library for half a year and read all important articles in our field, because then we would be done as original researchers. What’s your opinion on this, Cal?

  4. the worst mistake we could make is to go to the library for half a year and read all important articles in our field, because then we would be done as original researchers. What’s your opinion on this, Cal?

    I don’t know…at least in my little niche, the most original ideas tend to come out a deep understanding of the state of the art on the problem (which the original idea either recombines, or veers away from, in some interesting way). If you’re really out there on your own, it can be a steep hill to climb!

  5. Outstanding post! It’s way too easy to fall into a rhythm and unknowingly continue the same suboptimal work habits which inevitably produce suboptimal results. Do you have any thoughts as to how often one should perform or what external/internal factors signal that it’s time for an audit?

  6. Do you have any thoughts as to how often one should perform or what external/internal factors signal that it’s time for an audit?

    Study the people who are doing what you want to be doing, and then contrast their work habits with yours.

  7. Excellent post with several valid points! I always struggle to balance between all of my active projects, and did a similar audit at the beginning of this month. With Waveborn sunglasses sales almost non-existent during the fall/winter months, I have changed my focus to building a collaborative community for social entrepreneurs in the DC area at PunchRock ( My bank account could definitely use the additional revenue from subleasing our office space to new community members. At the same time, I’m spending more time on Georgetown’s campus coaching the ultimate frisbee team and giving my first classroom presentation in the business school next week on the importance of delivering strong elevator pitches. I have decided to shift my focus from sunglasses to teaching entrepreneurship and mentoring this fall, which I think will be beneficially for everyone involved. I also do 2 hours of personal development a day by reading various blogs/(e)books/etc, and I built out a large library of resources for entrepreneurs here:

  8. I’m in the middle of a “life audit” right now, and your thoughts have been really valuable to me. Thanks for writing a great blog with a unique perspective.

  9. Cal, I’m wondering if you’ve read the following article about different ways of approaching science(math) disciplines/sub-fields/projects and the different types of scientists(mathematicians) that seem to do best when working within an appropriate paradigm:

    At least in the molecular biosciences (my field), it’s harder to obtain and publish (make a good story about) field-establishing or paradigm-upsetting work, but the level of prestige obtained by doing so (Nature, Science, Cell, PNAS papers) is the highest. The meticulous refinement is totally necessary (and sometimes becomes paradigm-upsetting or redefining), but not always highly rewarded- especially at the funding stage. Many successful PIs I know try to balance some of each type (probably subconsciously), most likely by having at least a few different types of lab members who can focus on projects at different “stages” within the discipline.

  10. Excellent article, Cal. I’ve been diving deeper into habit formation recently and I’ve come to similar conclusions.

    When things go wrong, they often go wrong slowly. Taking a trip to McDonald’s “just this once” turns into once per week and then twice per week and then three months later you’ve put on ten pounds. I would argue that the same thing can happen with our work. For smart, creative people it can be easy to get excited about investigating new problems, but soon one speculative project turns into three or four and so on. If we let this process runs it’s course, then it’s easy to find ourselves in a less productive state. And that’s why a habit audit like yours is so critical.

    That said, I’m also curious about why we naturally choose more speculative projects rather than choosing to build on important work. I’m not sure, but one answer might have to do with our search for validation. Brilliant people want to be acknowledged as brilliant. We want our work to be significant. For that reason, it’s easy to see why we might pursue speculative projects. Who wouldn’t want to become known as the first person to solve a new problem?

    Because of this I think it’s critical to remind ourselves that important work is important because other people care about it. This seems obvious, but it’s all too easy for our egos to get in the way and find ourselves chasing new problems instead of building on work that people already care about. If we’re serious about doing work that makes a significant difference, then it’s critical to do habit audits and re-dedicate ourselves to doing work for others (or at least for the sake of our industry) rather than jumping at new projects that may seem sexier to us.

  11. I think I have a question somewhat similar to PhDHacker’s. I am a second-year PhD student in economics. I totally agree on the importance of a deep understanding of existing literature, but isn’t it true that besides the kind of breakthrough you mentioned by solving well-known and well-defined existing problems in the field, there’s another kind of breakthrough, the kind that bases on very original research and opens up new areas in your discipline? Do you think that reading existing literature and complementing it would be the best way to make this particular kind of contribution? It seems to me that the latter kind is not less likely to earn you a tenure than the first kind. Please excuse me if any of my analysis sounds off naive due to my lack of profound research experience. Thank you!

  12. Two thoughts:
    First: one of the top biologists in cell death research published this fun article about research in biomedical science. One of his key pieces of advice is to read lots, that new ideas come from knowing the literature really really well (his ‘thing #2’): or (for an abbreviated version)

    Second: I refer to Penelope Trunk who says that before you can think outside of the box, you need to know where the box is (surely a good way to do this is to read lots:

  13. Hi Cal, here’s some food for thought regarding different types of approaches in generating research:

    While the author lists some common strategies, there is no comment to how to mix it up to create a “portfolio” of active projects. I’m inclined to think of research in the same way as constructing a portfolio of stocks: more weight is put into mastering techniques to go deeply in existing results, while a small weight is put into speculative projects. Not the best analogy, but I guess in both stocks and research, things become clearer in hindsight.

  14. Hi Cal
    I just finished your book – both a wonderfully insightful and heartbreaking experience…heartbreaking in the sense that I realised I’ve spent the last 10 years of my working life ‘working wrong’ and find myself on the “plateau of acceptable performance” you speak of. What’s worse is that I’m burnt out and sense that the energy & focus required to aquire new & valuable skills are at an all time low. Thankfully I am still employed but know I need to apply some of your points in order to move forward in my industry which is undergoing considerable cutbacks and re-structurings worldwide. Without asking you to play life coach – any suggestions on how one might get better (not necessarilty so good!) at this point?

  15. Just got my first feedback on the Intro to my humanities dissertation at 250 pages, and the main driving point was that references need to be more heavily focused and concentrated on. He suggested 2 books that, though I’ve read them, were not cited. I think it’s going to be an easy problem to have, as I focused mostly on my own data, so most of my editing will be shoring up references. Very important idea.

    Another curious approach – what happens when you take away tenure as a motivator for research and work? More carrots, less sticks?

  16. mate. Killer book! Absolutely love it. Probably the most important book I’ve read bar the four hour work – which I know is divisive but it had a big impact on my life. Shared it with my dad and am recommending it to pretty much everyone!

  17. Cal, what’s funny about you bringing this up is that for a long time I was criticized by my peers for “screwing off” because I spend so much time reading literature related to my field of study.

    For a while, I stopped doing it because I wondered “what if I’m being too self-indulgent?” This went on for a while. Recently, however, I’ve been spending an extremely large amount of my spare time simply reading (I have a day job) and the results have been spectacular. Instead of staring at a blank screen in frustration for hours, I am absorbing new concepts like a sponge and the breakthroughs come to me completely naturally.

    Oftentimes, I’ll be writing up some notes on what I’ve been reading, go on a tangent, and then find that I’ve written 5 pages worth of extremely useful conclusions. What I’ve found is that spending too much time direclty “working” on something leads to trapping yourself in an echo chamber–I almost always find that my sticking points get broken because I read something that illuminated or rephrased a key concept.

  18. I read an excellent anecdote the other day regarding auditing and re-examining work habits. I can’t remember who it was, but they pioneered brick making production, a technology that has existed for thousands of years, by auditing and reconfiguring the process. The biggest single fix that was made, was to elevate the production table to chest height, thus eliminating hundreds of instances where the producer had to bend over. Brick production doubled.

  19. In my field of study (outside the walls of academia) – time management – the research is thin (there are no conferences, no journal, no departments of study and few committed researchers.) The field falls neatly between the cracks of a bunch of well-established disciplines.

    As a result, after reading and sharing the top 80 or so papers I have reached the bottom of the well, and have been forced to go elsewhere – into adjacent disciplines – to find further data, ideas, anything. So, I also recommend this approach – but it can truly look and feel like a waste of time. That is, until something clicks.

    Then, it’s all been worth it.

    Also, the work habits you described auditing in this post have to do with the content of your schedule, but you other more recent posts point to places where you are aggressively auditing the process that your work habits follow, also. I think the distinction is important to keep in mind.



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