Cal Newport's Blog, page 58

Impact Algorithms: Strategies Remarkable People Use to Accomplish Remarkable Things

(Image from WellingtonGrey.net via c2.com)

Impact Algorithms

I’ve been writing recently about the impact instinct — the ability to consistently steer your work somewhere remarkable. We know that diligently focusing on a single general direction and then applying deliberate practice to systematically become more skilled, are both crucial for standing out. But true remarkability seems to also require this extra push.

Since writing these posts, readers have sent me an amazing collection of quotes and articles that provide supporting details for this idea. Reviewing these resources, I noticed that the following systematic strategies — let’s call them algorithms — seem to pop up again and again.

Below, I summarize these algorithms, each of which I named for someone remarkable who exemplifies it: I don’t know that they’re all right; I don’t know which work best; but they should provide nuance to our understanding of the impact instinct.

The Feynman Algorithm

Nobel Prize winner Richard Feynman is a master of impact. Many people have attempted to understand his curiously successful approach (e.g., this wonderful collection of quotes that a reader sent me). Of the many candidates that might rightfully be called the “Feynman Algorithm,” here’s the one I think played the biggest role in his success:

Simplify the problem down to an “essential puzzle.” Here’s how Danny Hillis explained Feynman’s use of simplicity: “He always started by asking very basic questions like, ‘What is the simplest example?’ or ‘How can you tell if the answer is right?’ He asked questions until he reduced the problem to some essential puzzle that he thought he would be able to solve. Then he would set to work.” (Notice, the importance of simplicity is something we’ve encountered before.)
Continually master new techniques and then apply them to your library of unsolved puzzles to see if they help. As mathematician Gian Carlo-Rota explained when describing Feynman’s use of this strategy: “Every once in a while there will be a hit, and people will say: ‘How did he do it? He must be a genius!’” (Notice, it’s at this step of the Feynman algorithm that we see the value of ultra-learning.)

The Thrun Algorithm

Computer scientist Sebastian Thrun rocketed to fame when his self-driving car won the Darpa Grand Challenge (though his fame among roboticists long preceded that particular public victory). He now runs Google X, the search company’s skunk works for big impact projects.

Studying Thrun’s story, the following algorithm seems to be at the core of his remarkable accomplishments:

Pick a problem that matters. According to a recent Wall Street Journal profile of Thurn: “His mentor at CMU, Tom Mitchell, told him, ‘Pick a problem that matters to society.’ So he helped create robots, including a “nursebot” to assist the elderly in nursing homes and robotic tour guides…these were hard projects, [Thrun] says. ‘Just let go, trust your ability to learn, more [than] holding on to the things you’ve achieved—and that became the central theme in my life.’” 
Stick to it. The problems picked by start researchers who use the Thrun algorithm tend to be surprisingly generic — e.g., create robots that are good for society — but their clarity drives people to learn hard things, make hard connections, and wring the most out of their ability. This sounds obvious, but it really isn’t. The default behavior is, as Thrun warned, to “[hold] on to the things you’ve achieved.” Something needs to push you to keep breaking new ground.

The Erez Algorithm

Study Hacks readers know that Erez Lieberman Aiden, a hotshot young researcher out of Harvard, is my favorite example of the impact instinct. Recently, I’ve heard from several readers who know Erez, his advisors, and/or his academic field.  They pointed me toward the following important algorithm that he seems to use to great advantage:

Be Confident. “I knew Erez before he was a grad student,” a reader told me.  “And he was extremely confident then. Confidence and boldness pay off enormously in academia.” 
If You’re Not Confident, Do Everything You Can to Surround Yourself With People Who Are. This leaves the question of how one becomes confident. In the academic context, the readers who wrote me agreed that this confidence comes from surrounding yourself with people who are already doing remarkable things. “The cultural context here is really, really important,” said one reader. “Eric Lander and Martin Nowak [Erez's mentors] are powerful.” Another reader agreed: “These folks have grown up in groups/labs in which high impact papers are the norm. Not only do you pick up on how high-impact papers are written, but perhaps more importantly you develop the attitude that of course you can make high impact, such papers are something perfectly within your reach because they were routine in your scientific babyhood.” 
This Might Mean Getting “Good Grades.” We tend to separate remarkable accomplishments from conformist behaviors like studying hard, as the quest to become remarkable seems inherently rebellious. But a corollary to step 2 from above is that surrounding yourself with confident people often requires that you first jump through well-established hoops. If a freshman tells you that she wants to do research that will change the world, don’t tell her to go find a life changing project — she’s way too early in her development to successful apply the Thurn Algorithm — instead  tell her to earn the best possible grades, so she can can make her way  into a great graduate school, learn from the best people, and be surrounded by the most confident researchers. This is the foundation that produces remarkable things.

What You Know Matters More Than What You Do

Insight into Impact

I recently had an interesting conversation with some colleagues. We were talking about a young researcher in our field who happens to be absurdly productive — typically publishing four or five important results each year. In other words, this is someone with a highly-developed impact instinct.

As you might expect from a group of assistant professors, we were interested in figuring out his secret.

The easy answer is that he’s simply better than most people at solving hard problems. Perhaps where you or I might get stuck, he, in a flash of Good Will Hunting-style brilliance, taps the chalkboard four times and the proof is solved.

Some of my colleagues, however, have collaborated with this star researcher, and could therefore paint a more nuanced picture. He is quite talented, it turns out, but not at what you might expect…

According to my colleagues, this star researcher tends to begin with techniques, not problems. He first masters a technique that seems promising (and when I say “master,” I mean it — he really goes deep in building his understanding). He then uses this new technique to seek out problems that were once hard but now yield easily. He’s restless in this quest, often mastering several new techniques each year.

This sounds like an obvious approach, but it’s not. Most researchers are slow to adopt new bodies of knowledge — mainly because it’s really hard to do.

This star researcher, by contrast, is much more nimble — jumping from technique to technique, finding improvements and making connections.

What’s amazing about him, therefore, is not his ability to solve problems, but his ability to master things that are damn hard, damn quick.

The Ultra-Learning Hypothesis

Here’s something I’ve noticed more and more recently: this ultra-learning strategy is common in people who do remarkable things.

Richard Feynman, for example, used to brag about his ability to learn any topic in a short amount of time, a skill that led to one of modern science’s most breathtakingly diverse and important bodies of work.

Steve Jobs spent his career diving deep into topic after topic in his field — industrial design, operating systems, 3D graphics — so that he could see clearly what was possible.

And so on.

I hypothesize two things. First, ultra-learning is difficult but it can be cultivated. Second, it might be one of the most important skills for consistently generating impact. Those who are able and willing to continually master hard new knowledge and techniques are playing on a different field than those who are wary of anything that can’t be picked up from a blog post. (And yes, I recognize the irony of that statement.)

Both of these hypotheses might prove false. But what’s true is that they’re both deserving of more exploration.

Decoding the Impact Instinct

A Tale of Two Applied Mathematicians

Over the past few months, I’ve been working on an interesting research problem. My collaborator and I are taking some math tools typically used to analyze computer algorithms and are applying them to human behavior. Our plan is to publish in a specialized computer science conference. Because the work is different, we assume it might be an uphill battle to gain notice at first.

By itself, this story is not that relevant to our goal of decoding how people build remarkable lives. It gains new importance, however, when we contrast it to the actions of another researcher — someone with a phenomenal talent for remarkablilty, who once faced an eerily similar situation.

Six years ago, Erez Lieberman Aiden, then a 27-year-old Ph.D. student in a joint Harvard-MIT program, had a familiar idea. He also wanted to use the same math tools that interest me to study human behavior. Whereas I’m focused on a modern scenario (how people behave on social networks), Erez studied something more ancient (how cooperation evolved in early humans), but the underlying research strategy was essentially the same.

It’s here, however, that our stories diverge…

I’m targeting my results for a specialized venue and am still uncertain about its reception. Erez, by contrast, was more confident. He quickly wrote up his ideas and published them as a short note in Nature, one of academia’s most influential journals. The note might have been short, but its impact was long-lived: in the half-decade since it’s publication, its been cited over 550 times.

I’ve written in detail about the importance of diligently focusing on a small number of goals, and the importance of deliberate practice in developing skills fast. Erez certainly embraces these strategies. But then again, so do I. What strikes me is that there’s something more going on here. It’s as if Erez and I are, in some profound sense, wired differently in the way we choose and develop projects.

Put another way, he has an instinct for impact that I seem to lack.

At least, for now.

One of my new obsessions is decoding this instinct — how it works, and more importantly, how to cultivate it.

Failed Attempts to Dismiss the Impact Instinct

Let’s start by considering a pair of obvious explanations for Erez’s impact.

An easy dismissal is to defer to brilliance . Perhaps his secret is that he applies an absurd amount of brain power to solve important problems that stump his peers. If this is true, then there’s nothing easily replicatible about the impact instinct.

Fortunately, a closer look at his Nature paper falsifies this hypothesis. The result in the paper is shockingly straightforward: easy mathematics applied in a very natural way. (Erez even uses the word “simple” in the paper’s title to emphasis its lack of technical fireworks.) It was the basic concept he presented, in the way he presented it, at the time that he presented it, that mattered here.
Another easy dismissal is to defer to luck . Maybe he stumbled into an easy problem at the exact right time and is now reaping the unexpected windfall. If true, this too would yield a non-replicatible explanation for his success.

Fortunately, a closer look at Erez’s publication record falsifies this hypothesis as well. It turns out that he’s repeated this feat of producing a big impact result on two more occasions since his first breakthrough. Not only were these subsequent results in two different fields – molecular biology, and the quantitative study of culture – the corresponding papers both made the cover of  Science – an absurd success rate!

If we cannot easily dismiss Erez’s instinct as something impossible to replicate, we are left with a pressing question: what does matter?

Decoding the Impact Instinct

I don’t have a definitive answer to the above question, but I’m starting to circle around some likely suspects. Something that definitely catches my attention at this point are the specifics of Erez’s training.

Erez trained under Eric Lander, the MacArthur Genius Grant-winning director of the Harvard/MIT Broad Institute. Lander is an Oxford-trained mathematician who helped spark the convergence of math and biology that led to breakthroughs like the sequencing of the human genome.  He’s arguably the world’s top expert on applying mathematics to new areas of biology in a way that generates high impact results.

Training under Lander, a young Erez would have been taught exactly what type of novel interdisciplinary results cross the threshold required to publish in Nature, and how to write and promote such results in a way that demands attention. (In fact, in my new book on remarkable careers, which comes out this September, I profile a hotshot young Harvard professor who, like Erez, also mixes mathematics and biology in attention-cathcing ways, and who also did a postdoc in Lander’s lab. She too made her reputation with an influential Nature article while still working under Lander.)

I have no idea, for example, how to take the computer science result I’m working on and shape it so that it can be published in a top general science venue, like Science or the Proceedings of the National Academy of Sciences, or so that it can gain major press attention like Erez often wins for his results (c.f., this cover article in the New York Times). To me, to attempt to do so seems like a wasted, hubristic effort.

Hypothetically, however, if Eric Lander revealed himself as a huge Study Hacks fan, and  flew down to D.C. to personally coach me, I wonder if these goals would suddenly become plausible?

In some sense, on a smaller scale, I might already be benefiting from a similar coaching advantage. I frequently publish at a conference called PODC, which is a top venue in my niche of distributed algorithm theory. It undoubtedly helps that my PhD advisor at MIT founded the conference. My whole graduate training was oriented around the goal of “writing PODC papers,” much in the same way I assume Erez’s training was oriented around “writing attention-catching Nature and Science papers.”

If this training-centric hypothesis is correct, it bring us back to my recent interest in avoiding pseudo-striving and embracing reality-based planning. Lots of very smart researchers want to replicate the type of success enjoyed by Erez Aiden Liberman, and most work just as hard. But they’ve failed to put an equal emphasis on figuring out how to direct this energy toward impact. We all chat casually about this topic, but what I see in Erez is a systematic, non-obvious, difficult training in these realities.

We can’t all go work with our fields’ equivalents of Eric Lander, but I don’t think this prevents us from learning the same lessons about producing impact. My optimistic contention is that if we apply a touch of the journalistic to our careers — systematically studying, without bias toward what we want to hear, the reality of how our colleagues gain notice — we can hone the type of instinct that Erez deploys so effortlessly.

Bottom Line: There’s no magic in how these stars become remarkable, but there’s nothing simple here either. Stand outs like Erez were trained by world experts in how to produce impactful results in their field. This training is crucial and non-obvious. If we don’t work hard to replicate it, we cannot expect to replicate its results.

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I’ll talk more about my new book as we get closer to the September publication date, but if you’re interested in learning more in the meantime, check out Publisher Weekly’s nice review, which came out earlier this week, or this recent Wall Street Journal article that quotes me on some of the book’s ideas.

(Photo of Erez at TED Boston by Ritterman)

Some More Thoughts on Grad School

Re-Reflection

In 2009, as I was approaching the end of my Phd program, I wrote a blog post titled, Some Thoughts on Grad School. It described lessons I learned during my time at MIT.

Since then, I’ve received many requests to revisit the theme. Now that I’m a professor — albeit a new one — I thought I’d once again reflect publicly on what I did well and what I wish I’d done better.

With this in mind, I want to offer a pair of thoughts on a topic of particular importance to my path as an academic: complexity.

Thought #1: Avoid Complexity When Seeking Problems

Early in my graduate school experience, I had a mentor named Rachid — a well-known distributed algorithm specialist from EPFL. I learned many things from Rachid. For example, I once asked him for advice on a summer internship I was considering. I made different arguments  about the value of gaining connections and learning about industry.

“If you want my personal opinion,” he replied, “your time is better spent at MIT, preparing the next STOC/SOSP/JACM paper.”

To put this in context: STOC, SOSP, and JACM are acronyms for some of the most elite conferences and journals in the field of computer science. The lesson Rachid offered — which I’ve since strongly embraced — is that in the end, hard results are all that count.

But the Rachid lesson I want to emphasize here is about the danger of complexity. His approach was to always reduce a problem to its purest, most simple form. This is what leads to true understanding of the mathematical reality underlying the issue, he believed. Once you’re armed with this understanding, you can then, and only then, add back details (and the complexity they require) with confidence.

If you want to see this philosophy in action, take a look at this paper I co-authored with Rachid and another graduate student from MIT. The big picture problem that interested us was messy: how do parties work together to solve problems when their only means of communication is a broadcast channel where a malicious adversary can both jam and spoof messages?

You’ll notice in the paper, however, that we immediately reduce this down to the simplest possible expression of what makes this setting difficult: two players, Alice and Bob, trying to communicate a single bit, while a third player, Collin (the collider), tries to disrupt things.

All of the results in the paper build on our deep understanding of this simple three-player game.

(For what it’s worth, the paper has since been cited around 50 times.)

The problem here is that most graduate students tend toward the opposite of this approach. Their biggest fear is that they’ll propose a result and someone more knowledgeable will look at it, declare it “trivial,” and therefore validate their nagging imposter syndrome. Accordingly, students tend to rush to add technical complexity right away, as if a page full of math validates their ability.

This approach is flawed because it’s hard to make an impact in a technical field without deep understanding, and it’s hard to build deep understand of anything that’s not dead simple to describe. This is why the most respected professors are often those who are most likely to interrupt you and say, “slow down, and explain this to me like I don’t understand anything.”

They don’t want equations, they want insight.

Bottom Line: Hold off complexity as long as possible when studying a problem. It will inevitably enter the scene, but the later the entrance, the more insight you’ll develop.

Thought #2: Seek Complexity in Your Technical Skills

My first thought concerned something I think I do pretty well. My second thought concerns something I didn’t do enough as a graduate student, and that I’m only now, painfully, learning to embrace.

The value of a graduate student (not to mention, an assistant professor), I’ve come to realize, is directly proportional to the quantity and complexity of their technical tool kit. If you study algorithms, for example, the more corners of the literature you’ve mastered, and the more mathematical analysis techniques you’re comfortable with, the more problems you’ll be able to solve. And the more problems you’re able to solve, the more likely that you’ll solve some hard ones — the key currency for an academic career.

This thought doesn’t contradict the first thought (though it might seem to). When tackling a problem, you want to start with its simplest expression. To find a good problem and then make sense of its simplest expression, however, you need the most powerful possible combination of knowledge and skills.

The trickiness here is that mastering new knowledge and learning new technical skills is like learning to play a new instrument: it’s difficult, and frustrating, and takes a long time.

All graduate students are forced to develop a basic tool kit due to the deliberate practice required to pass your courses and contribute to your first publications. The students that thrive, however, don’t stop there; they keep pushing themselves to learn more.

I didn’t do nearly enough of this.

It took me two years to get decent at solving a certain class of problems concerning deterministic distributed algorithms (roughly 2004 – 2006). There was then a two year period where I was satisfied to use only this hammer and go seek nails, no matter how hard they became to find.

The issue I faced was that my field was moving forward. Randomization was where the interesting new work was being done, and my approach was in danger of becoming dated.

It wasn’t until 2008 that I began the dreary effort of teaching myself probability theory. In this early paper, for example, you can see the beginning of the transition: the majority of the results are deterministic, but they draw on a tentative, randomized sub-routine. (This is where, for example, I reintroduced myself to Dr. Chernoff).

The next year I published this paper, which pushed me forward in my learning, but was also a terrible strain. A significant fraction of its results came from the following process:

I would get stuck because I didn’t know enough probability theory.
I would go talk with one of my co-authors, who would reply by filling a white board with a bunch of inequalities.
I would scramble back to my office and try to recreate the argument from scratch, filling in the details, before it slipped my mind.
I would return to my co-author to discover that I had fouled up my dependencies in some terrible way that would likely involve the intervention of something called a “Martingale.”

This was pretty brutal. But I learned quite a bit.

I am realizing now, however, that my pace was still too slow. For example, I should have shot past independent probabilities and mastered techniques for bounded dependence. This is a natural — though difficult — next step that I avoided for too long.

Over the past year, I’ve been systematically increasing my pace of skill learning (more on this soon), but if I had committed to this mindset with more purpose back in 2006, I’m embarrassed to think about the extraordinary impact on my work it might have had by now.

Bottom Line: Treat your time as a graduate student like a professional musician treats his or her performance repertoire. If you’re not constantly straining yourself to learn more and perform better, you’re in danger of being left behind.

(Photo by Nietnagel)

Facebook’s COO Works Less Than You

The Fixed Schedule Phenom

Sheryl Sandberg is the COO at Facebook.

Last year she was paid over $30 million dollars in stocks and salary.

This year she was named to Time magazine’s 100 Most Influential People in the World list.

But here’s what interests me most: in April she revealed that she leaves work every day by 5:30. She has practiced this habit since she first had kids, but only recently did she build enough confidence to talk publicly about it.

This is a fantastic example of the fixed-schedule productivity philosophy that I’ve long preached. As many have discovered, fixing strong constraints in your working life can paradoxically make your work much stronger (as it forces you to focus on what’s important, which in turn helps you get better at what you do).

E-mailing during every waking hour might make you feel more important, but as Sandberg’s accomplishments verify, it has very little to do with your actual impact.

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Speaking of interesting articles, my friend Elizabeth Saunders has a thought-provoking piece on the Harvard Business Review blog about the different types of passion and their implication for our working lives.

 

Do What Works, Not What’s Satisfying: Pseudo-Striving and our Fear of Reality-Based Planning

The Dune Revelation

In July 2009, I took a trip to San Francisco. At some point, I ended up hiking at a sand-duned nature preserve, not far south from Monterey on Highway 1.

What I remember about this hike is a thought that struck not long into the route. In the summer of 2009, I was two months from defending my PhD dissertation. I had arranged for a post doc after graduation but found the academic market beyond to be uncertain for me and my skills. It was in this context that I had my insight:

Why hadn’t I systematically studied the most successful senior grad students when I first arrived at MIT?

Every year, a small number of computer science students at MIT easily generate multiple job offers while the rest have to sweat the process. What do these students do differently from the others? It’s a basic question and yet almost no one arriving in Cambridge seeks an answer. We instead carve out our paths blindly, sticking our heads up only at the end to see if we’ve stumbled anywhere near our destination.

I ended up fine, landing a great tenure track position at Georgetown, but the 2009 version of myself did not have this certainty, and my failure to more systematically plan for my arrival on this market suddenly seemed a glaring omission.

The $100 Startup

This 2009 experience came back to me earlier this week as I read an advance copy of Chris Guillebeau’s new book: The $100 Startup. In this book, Chris tackles a topic made popular by Tim Ferris: how to build a lifestyle business in a digital age.

Lots of people are enamored by the idea of having a business that requires little investment and yet supports you financially while injecting flexibility into your life.

What sets Chris’s book apart, however, is that he was not content inventing a bullet-point system that simply sounds good. He instead systematically studied people who had actually made these types of businesses work. He started with a survey of 1500 such entrepreneurs which he then narrowed down to 100-200 that he interviewed in more detail. He lists them by name in his appendix.

The result is often messier than the internally-consistent, inspiration-boosting acronmyized systems of competing books and blogs, but the advice come across with an authenticity that’s rare for this topic.

Put another way: Chris did with his interest in lifestyle businesses what I should have done as a grad student with my interest in becoming a professor. The only plan he was interested in was a plan grounded in reality.

The Big Question

I’m telling these stories because they inspire an important question: Why do so few people do what Chris did? Most of us are content, it seems, to work hard and build complicated systems, but we avoid basing our efforts on a reality-based assessment of what really matters.

And I think I finally have an explanation…

The Pseudo-Striving Hypothesis

Why do so many ambitious people approach their quest for remarkability in the way I approached grad school, and not in the way Chris Guillebeau approached lifestyle entrepreneurship? Here’s my tentative explanation:

The Pseudo-Striving Hypothesis

It’s significantly more pleasant to pursue a goal with a plan entirely of our own construction, then to use a plan based on a systematic study of what actually works. The former allows us to pseudo-strive, experiencing the  fulfillment of busyness and complex planning while avoiding any of the uncomfortable, deliberate, often harsh difficulties that populate plans of the latter type.

For example…

For the aspiring writer, embracing National Novel Writing Month is pseudo-striving. It feels good to sit down every morning and throw a few hundred words on a page. But the reality of writing would tell you that getting your fiction chops to a publishable level requires the training that comes only in the form of writing for someone else — be it an MFA classroom or edited publication. You need the fear of rejection to push your writing skills. Then you still need to experience that rejection time and again during the period where your skills are just starting to improve. It’s much easier to sit on your deck with your MacBook and a cup of coffee and applaud yourself for your dedication.
For the aspiring grad student, seeking research ideas that fall comfortably within the scope of what you already know how to do, and then trying to convince other people that your work is important, is pseudo-striving. Reflecting on my experience, I notice now that academia is much more likely to reward the strategy of spending the 12 – 24 months of deliberate practice necessary to master an important emerging field. This is really hard. But those who persist end up doing work with impact.
For the aspiring lifestyle designer, dedicating hours to e-mail auto-responders, WordPress widgets, and social network engineering is also pseduo-striving. It gives you lots to do, nothing is really judged a success or failure, and nothing is really hard, but you feel engaged and active. It’s quite pleasent. Many of the successful entrepreneurs from Chris’s book, by contrast, had a reality-based fixation on actually making real money from real people before doing anything else (be it leaving their job or optimizing a web site). This is less pleasant, because you might fail time and again to convince people to give you their money, but ultimately it’s all that matters, so that’s where your initial energy should be focused.

Conclusion

When it comes to constructing a remarkable life, I’m increasingly convinced that pseudo-striving is a common trap with devastating consequences. It lulls you into a rhythm of busyness and complexity that might have very little to do with real accomplishment.

I’m not sure why our instincts lead us to flee reality-based planned, but they do. The more explicitly we recognize the difference between pseudo-striving and the messy difficulty of real world accomplishment, the better, I hope, we can refocus our efforts onto what matters.

(Photo by rooksbane)

Walking in Merlin Mann’s Footsteps and a Book You Should Know About

Two brief administrative notes…

A2 Earns an A

When I first started blogging in 2007, I needed web hosting. I noticed that Merlin Mann had a note on 43 Folders about his happiness working with a company named A2 Hosting. That was good enough for me: I signed up for their introductory package.

That was five years ago and I’ve been nothing but happy with their service ever since.  Now, in a nice bit of circularity, they’ve agreed to sponsor Study Hacks in much the same way they were sponsoring 43 Folders back when I got started with blogging.

So if you’re looking for web hosting, you have my recommendation.

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Community College Success

Speaking of recommendations, I have one more to make. An important segment of my readers is community college students. I like these students because they are often way more pragmatic than their counterparts at four year institutions. They see school as an investment and want to get the most out of the money they put in, and therefore they tend to focus more on the nitty-gritty of their strategies (which I enjoy) and less on whether their major is their passion (which I don’t enjoy).

Anyway, a shortcoming of my student writing is that I’ve never done systematic studies of community college students, so my advice in this area is somewhat tentative.

This is why I am happy to enthusiastically recommend Isa Adney’s new book: Community College Success.

If you’re in community college and are looking for advice tailored to your specific setting, Isa’s book is a great place to start.

 

The Father of Deliberate Practice Disowns Flow

Feeling Low on Flow

In a trio of recent articles, I emphasized that flow is dangerous (see here and here and here). It feels good, so we’re tempted to seek it out, but it doesn’t actually help us get better: the key process in creating a remarkable life.

Most of you liked this concept, while a few of you thought I had missed the boat. Here’s an example of the latter sentiment:

I disagree with [your] point. Flow is the experience of being lost in one’s effort. That can easily happen when one is highly challenged and enjoying the intense effort.

There was also quite a bit of discussion on what, exactly, “flow” means, with enough different points of view presented that I soon felt that the whole issue was becoming muddied and difficult to wade through.

Then someone sent me an article penned by Anders Ericsson — the psychologist who innovated the study of how we get better by introducing the idea of deliberate practice. In this article, which was published in 2007 in the journal Current Directions in Psychological Science, Ericsson addresses the difference between flow and deliberate practice:

It is clear that skilled individuals can sometimes experience highly enjoyable states (‘‘flow’’ as described by Mihaly Csikszentmihalyi, 1990) during their performance. These states are, however, incompatible with deliberate practice, in which individuals engage in a (typically planned) training activity aimed at reaching a level just beyond the currently attainable level of performance by engaging in full concentration, analysis after feedback, and repetitions with refinement.

In other words, the feeling of flow is different than the feeling of getting better. If all you seek is flow, then you’re not going to get better. There is no avoiding the deliberate strain of real improvement. (This is not the say, however, that you should not seek flow in addition to deliberate practice as a strategy to recharge, or experience it as unavoidable when you put your deliberately honed skills to use.)

Ericsson concludes by echoing a warning familiar to Study Hacks readers:

The commonly held but empirically unsupported notion that some uniquely “talented” individuals can attain superior performance in a given domain without much practice appears to be a destructive myth that could discourage people from investing the necessary efforts to reach expert levels of performance.

He said it. Not me.

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This post is part of my series on the deliberate practice hypothesis, which claims that applying the principles of deliberate practice to the world of knowledge work is a key strategy for building a remarkable working life.

Previous posts:

The Satisfying Strain of Learning Hard Material
Beyond Flow
How I Used Deliberate Practice to Ace my Computer Science Final
Flow is the Opiate of the Mediocre: Advice on Getting Better from an Accomplished Piano Player
Is Talent Underrated? Making Sense of a Recent Attack on Practice
Perfectionism as Practice: Steve Jobs and the Art of Getting Good
Complicate the Formula: John McPhee’s Deliberate Practice Strategy
If You’re Busy, You’re Doing Something Wrong: The Surprisingly Relaxed Lives of Elite Achievers

(Photo by Kofoed)

The Satisfying Strain of Learning Hard Material: A Deliberate Practice Case Study

A Deliberate Morning

This morning I finished my notes for an upcoming lecture in my graduate-level theory of computation course.

There are two points I wanted to make about these notes…

The process of creating them is very hard. On average, it takes me between 2.5 to 3 hours to prepare a lecture. This preparation requires that I work with absolutely zero distractions as the material is too difficult to be internalized if my attention is divided in any way. Furthermore, the work is not particularly pleasant. Learning things that are this hard does not put you in a flow state. It instead puts you in a state of strain, similar to what is experienced by a musician learning a new technique.
I have gotten better at this process. The lecture I prepared today was the twenty-first such lecture I have prepared this semester. The earliest lectures were a struggle in the sense that my mind rebelled at the strain required and lobbied aggressively for  distraction. This morning, by contrast, I was able to slip into this hard work with little friction, tolerate the strain for three consecutive hours, then come out on the other side feeling a sense of satisfaction.

Recently, we have been discussing the deliberate practice hypothesis, which argues that knowledge workers can experience big jumps in value if they apply deliberate practice techniques to their work. My three-month experiment in timed, forced concentration provides a nice case study of this idea. I am now better at mastering hard concepts than I was before. The mental acuity developed from this practice translates over to the research side of my job, helping me more efficiently understand existing results and more deeply explore my own ideas.

To toss the ball back in your court, imagine what would happen if you replaced “graduate-level theory of computation” with a prohibitively complicated but exceptionally valuable topic in your own field, and then tackled it with the same persistence…

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This post is part of my series on the deliberate practice hypothesis, which claims that applying the principles of deliberate practice to the world of knowledge work is a key strategy for building a remarkable working life.

Previous posts:

Beyond Flow
How I Used Deliberate Practice to Ace my Computer Science Final
Flow is the Opiate of the Mediocre: Advice on Getting Better from an Accomplished Piano Player
Is Talent Underrated? Making Sense of a Recent Attack on Practice
Perfectionism as Practice: Steve Jobs and the Art of Getting Good
Complicate the Formula: John McPhee’s Deliberate Practice Strategy
If You’re Busy, You’re Doing Something Wrong: The Surprisingly Relaxed Lives of Elite Achievers

“Being Very Good at Anything Involves Being Somewhat Addicted”: Hard Truth on the Sheer Difficulty of Making an Impact

The Chess Master and the Economist

A reader recently sent me an interesting interview with Ken Rogoff, a hotshot economics professor at Harvard.

As a young man, Rogoff was a world-class chess player. He eventually translated his ability to grad school where he studied economics with a focus, naturally enough, on game theory. What caught my attention in Rogoff’s interview was his dedication to diligence.

Even two interests, in Rogoff’s thinking, represented one too many:

[A]t graduate school he became convinced that dividing his attention meant that both his chess and his economics were suffering. He had to make a decision. [He chose economics.] “Part of my strategy of moving on was to give it up completely. I don’t play chess casually…Not unless it’s incredibly rude to decline playing.”

He elaborates:

“Being very good at anything involves being somewhat addicted.”

Bottom line: I am increasingly stricken by the yawning gap that exists between the feel-good, follow your passion, be the change you want to see-style chatter that fills the online world, and the reality of how people actually end up making a true impact.

(Image by jojoivika)