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.
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)
44 thoughts on “Decoding the Impact Instinct”
Just because his results are simple doesn’t mean it was simple to arrive at them. Creative genius often yields simple, self-evident results, merely by seeing solutions other people couldn’t.
This is going to sound rather obvious, but if I was in your position, I’d just call Aiden and/or go and see him and ask your questions. If that fails, email Lander. [I assume the former’s time is easier to get hold of.]
Sorry, I pressed submit too early. The point wasn’t just to call them, but that things like “impact” seem to be, to me, a skill that humanities based people are much better at – it either comes naturally or with practice, but it seems to be something that scientists find a lot harder to do. [Yes, I’m generalising] Also, I like your honesty in showing that there are things you do not know. Many bloggers wouldn’t ever admit something like that, no matter what the subject is.
Hi Cal, a common theme in the big academic successes that you’re talking about seems to be their interdisciplinary nature. I know that you’ve advised in the past to focus on only a single area, so I was just wondering if you had any thoughts on what to do to promote these cross-discipline insights. Thanks!
Another interesting thing to note about Erez Aiden is that his pre-PhD studies included a bachelor’s in philosophy, “certificates” in “applied and computational science” and in “environmental sciences”. He also studied for a master’s degree in history. He also took a mere four years for his undergraduate studies.
What can be inferred from this? Quite a number of things and one of those is that he can “juggle” with very different fields and it is possible that his ideas came (to a certain extent) from the various things he kept on reading. If he spent four years studying for so many qualifications and doing exceptionally well, I suppose that it can be assumed that he kept on doing the same after.
Great post, Cal. I’m really looking forward to your new book and just wanted to say thank you for your advice throughout the years. I’ve followed your blog since the beginning of my college career and it has been tremendously helpful – actually, that’s an understatement. Your ideas completely transformed the way I viewed success and helped me not only academically but also in other areas such as learning the piano. I’ve also gained a lot more confidence in myself as opposed to attributing other people’s success to innate brilliance. I’m now a senior in college applying to law school and I can honestly say I wouldn’t be where I am now (basically doing things that I wouldn’t have envisioned myself doing only a few years ago) thanks to your advice. So just wanted to say a sincere thank you and I look forward to your upcoming work!
I wonder if another way of looking at this (which might be equivalent to what you are saying) is that modelling a high-impact paper (i.e., determining and then copying the salient features) is a hard-to-master skill, which can be achieved through deliberate practice?
The editors of Nature itself are probably the people with the best idea in the world of how to get a paper accepted. Maybe speaking with them or editors of other high impact journals would be fruitful?
I had this idea in the back of my head to try and find patterns in the way that papers in high impact journals build on previous work in their fields, but it’s hard to do without background in the specific field. And I lack background in any specific field.
This is a really interesting problem, and I think the solution might really be very simple (and not in a non-replicable way). I’ve been reading your blog for a long time and you always have a lot of interesting ideas. I’m glad you brought this up.
So, the difference I see between the two ideas “how people behave on social networks” and “how cooperation evolved in early humans” is that… well, the second idea is something that it is much harder to not care about. It is hard to hear about a problem as basic as human cooperation and be like, “so what? who cares?”. But I could imagine someone maybe being like, well… social networks? what if there were no social networks, would we care about how people behave on facebook then? (I mean, I think it’s interesting, but the fact is you might be giving too much room for other people to brush it off.) I think to guarantee huge interest, the idea has be crystallized further. You have to keep asking why it’s interesting, until you get the base, instinctual level of what makes the problem so compelling. And then realize that that is the real problem you are solving. Don’t leave room for others to wonder why your idea is important. I think you have to just “ask enough whys” ahead of time so that your audience isn’t forced to ask any whys themselves, because if they have to ask why it’s interesting, they can decide it’s not. The second idea is more crystallized because I imagine maybe before he realized he was interested in the evolution of cooperation, he was studying something more abstract, like I don’t know, some kind of randomized greedy algorithm or something, and he stopped to be like, but why do I think this is interesting? Who cares about randomized greedy algorithms except for a bunch of course 6 kids and their professors? Because these algorithms are important for understanding how to make systems efficient. Or how systems evolve to become efficient, etc. So what’s so interesting about that problem? etc, etc and I think he kept asking why until he got to a problem even his grandma would be interested in. I mean, I have no idea if that’s what he actually did, but I think that’s what the process would feel like.
Anyway, the point is imagine a dinner table where there are like, ten of your peers, some of whom have a vague but positive opinion of you, and the rest are either your enemies or have their own agenda and just don’t care about you. Imagine they’re trying to decide who to vote off the island. If ANYONE at the table says, let’s vote off Cal, I hate that guy, it’s very hard for your vaguely friendly acquaintances at the table to stand up for you. So you get screwed. You have to be the guy that no one wants to even try voting off the island, in order to not get voted off the island.
I had the thought recently that maybe the point of any thesis or research paper, etc is ultimately to convince people that the problem you have defined and motivated is an interesting one. it’s ultimately a story that’s like, seriously guys, this work is a big deal because look at all these background papers, it’s clearly always been a big deal to humankind and I’ve done just a little bit of the work right here that pushes this field forward and these are great results but we are just getting started, there is a lot more that can be done and here are some further steps that other people can take to keep working on the problem I’m working on. It is ultimately about making other people care about the same things you care about.
Nature receives around 200 submissions a week and accepts about 8% of that. You are notified in 1 week whether your article will continue to the next steps of review.
It doesn’t seem impossible… What would Tim Ferriss do?
Hi Cal, You’re the best. Among other things, you openly tackle challenges many people are afraid to say they think about. Your “impact” question, however, seems to me to be related, in a way you have not mentioned, to your view that undergraduates should choose the best possible Ph.D. program, with the best possible professors. You do not mention by name the value of plain old conversation.
I think that developing a skill for “impact” results partly from sitting in on the best conversations. Applying to the best graduate program is not just, in my view, a route to good research topics or to references that will help get a job later on. (Nor did you say that it was.) To me, however, being in the best program is a way to listen in on the best conversations. I had the advantage as a graduate student in linguistics long ago of sitting in on many conversations among the most brilliant people in the field, including those at MIT, where I spent my dissertation year. When you are in on–even listening in on–the best conversations, one potentially useful idea follows another naturally. Because as speaking human beings we have a tremendous drive to take part in the conversation around us.
PS. I just got back from giving a workshop on the topic of that book that I would not have finished without daily recitation of your motto “Get to be so good they can’t ignore you.” Thanks, again. MCG
What you frame as “training oriented around” may just be mimicry (you write to please your boss) plus social connections (your boss is famous among the target gatekeepers so you get a halo effect).
(I liked your comment, Lily.)
Cal, have you ever thought about switching from CS into psychology? It seems to me like you are more obsessed with studying experts and achievement than studying CS. Maybe I’m just biased in my understanding of you because you don’t have a CS blog to show us that obsession as well.
But let’s look at your description of yourself: “I’m a 29-year-old computer scientist interested in why some people lead successful, enjoyable, meaningful lives, while so many others do not.” It’s interesting that you basically say that you’re a Computer Scientist who is interested in a non-CS topic and then you don’t list any CS topics. Of course this description is for the blog so it’s a description skewed in favor of Patterns of Success so that’s a biased data sample.
I feel like your crazy obsession with Patterns of Success is exactly what you need to publish successful papers in the field of psychology. Isn’t what this whole thing is leading up to? The moment of insight when Cal realizes that all of the evidence points to switching fields! It goes against your theory that following your passion is not necessarily the best choice and that the real successes build remarkable lives.
I like your blog and I’ve read it for a while. I even read your older posts. I am kind of amazed that you’ve been obsessed with psychology for so long. (hint hint 😉
I think you need Psychology and Psychology needs you.
What do you think?
I really enjoy this blog. I find it both helpful and though-provoking for aspiring academicians. I am a graduate student in chemistry and we are currently wrestling with reviewers to get some results into the higher tiered journals. We stumbled across these highly impacting results very serendipitously. The struggles we’ve had to get them published make me wonder even more so about those PIs that just can’t stop publishing in Nature or Science. Your post has provided some nice insight.
I’ve provided a link that I find helpful. It is an interview of George Whitesides, a renowned chemist at Harvard with something like 1100 publications, a large percentage of which I would consider high-impact publications. As he gives a new graduate student a project he also gives them a book on writing and asks them to begin working on the manuscript as they begin experimenting. I would love to hear your thoughts on this. Thanks for the great blog!
Sorry I put the link in the website box. Here it is below:
Cal you’re a smart guy but you missed a another obvious explanation: The good ol’ boy network. When I worked at a political consulting company I was shocked at how many doors opened for me just because of who I worked for. My guy didn’t even need to make any calls, everyone just knew who I was connected to. Erez may not have any special tricks – just having Lander’s name behind him may be enough to affect his impact at getting published.
I find this particular post discouraging because I don’t agree that publishing in Nature or Science means that you have “impact.” Maybe this is just something that bitter professors say, but I have heard many times that publishing in these “top” journals is as much related to politics and who you know as it is to the quality and importance of your work. It definitely seems like some fields would have a harder time publishing in these journals than others, so is it really fair to say that Nature and Science publications should be the dream goal for all scientists?
This is an interesting concept…
Music to my ears…
Not music to my ears. If you’re applying to law school simply because it has a clear path and is competitive, that’s not a good enough reason.
I think you’re definitely on to something. This also dovetails nicely with Erez’s background in the humanities. He might be more comfortable with assessing impact than most nerdy, results-obsessed scientists.
Good question. I assume he’d find a way to observe the process of those 8% that succeed.
I like this way of putting things.
By the way, I have your book on my shelf here next to me at my office.
Given that you’re only exposure to me is my blog on decoding patterns of success, I can see how you might think that I only think about decoding patterns of success. The reality is that I spend about 3 hours a week, on average, on this blog. The amount of time I spend on my job as a professor is, as you might suspect, considerably larger.
You can consider my publication record my CS blog…
I don’t buy it. My experience in academia is that the best stuff, more or less, gets published in the best places. Complaints about luck and connections tend to be just bitterness…
That is true. I’m using SCIENCE and NATURE as a placeholder for impact, not necessarily the only way of measuring this trait.
I think you cut right to the issue when you noticed that Eric Lander simplified. He didn’t try to publish an unimpeachable piece of work. He just wrote up his idea in its most distilled form and published it.
In my experience, moving that quickly is INCREDIBLY uncomfortable because you are constantly churning out raw work that you haven’t had time to fully consider. You never feel that your idea (or you) are “ready” to be seen. But if you hold yourself back you’ll be overtaken by people with a similar ideas who push forward despite uncertainty.
Could it be that Erez Lieberman Aiden’s work has had impact because his work is focused on his subject not on making an impact with his work? And could it also be that there was a convergence of factors at the time of his first publication: interest in the subject, lack of previous published material on the subject, …kismet???
My suggestion is this:
1.Pick 3 to 5 posts from the Study Hacks blog that you think best present your philosophy of life and success (or alternatively: write an essay on the same topic);
2. write to Erez and other people you admire and ask them to read those posts (or essay) and request for their input on what they think you’re doing right or wrong (as far as life and success go, or anything else they find relevant);
3. hire a professional personal coach or consultant and have them evaluate your philosophy of life and success.
In other words: Instead of you trying to figure out successful people, sometimes have successful people (or people who are in the business of evaluating success)assess you.
I’m not sure if I get this point. Aren’t all scientists focused on their subjects?
I interviewed a lot of people like Erez for my new book, so you’ll be seeing some of that wisdom soon. (Something to keep in mind is that many of the questions I ask here are semi-rhetorical; I am trying to getting a better understanding of the impact, but I do have a lot more research to discuss and draw from then I may have been letting on.)
Coaches, on the other had, are a waste. They basically act as an accountability mechanism. If, however, you’re not putting your attention on the right things, the accountability doesn’t help, and if you are, you don’t need someone else’s prodding to do those things.
I agree with Frances – there is the dichotomy between focusing on one’s subject and focusing on making an impact.
Focusing on one’s subject is a matter of one’s personal expertise.
Focusing on making an impact is an attempt to engineer a particular response from people – and that is already in the realm of manipulation. People tend to pick up on that and respond negatively.
Focusing on making an impact suggests that the person is trying to make up for some painfully felt personal deficiency.
If Bill Gates, David Allen, or Erez Lieberman Aiden would read about your philosophy of life and success, what would they comment on it? How would they evaluate it?
I live in a nice McMansion bought with the wisdom of learning how to work the political side as well as the technical side, so I’m not complaining, I’m trying to alert you to another explanation. I’m not saying this is the only explanation, just that it should be explored along with “brilliance” and “luck”.
Maybe scientific journals really are paragons of meritocracy, but all technical fields are still run by humans and humans are political animals. Call it something more palatable if you like, but salesmanship is a big part of science.
Erez is not trained by Eric Lander, he works mostly with Martin Nowak.
Good clarification. But probably the same note idea about expert training applies…
David Allen wouldn’t mind, but Gates and Aiden might be baffled. In general, I’ve found that distilling experience to systematic axioms is a practiced skill. People who may have deployed some strategies implicitly to be successful often cannot clearly articulate or even recognize those strategies, unless they are in the habit of doing so.
That being said, it doesn’t mean that these strategies always exist. I have to assume that some notions of success are more decodable than others, and I don’t know which is which! Part of what makes this project suspenseful…
Isn’t the take-home lesson that Erez got his idea published in Nature (and had a big impact) simply because he was the FIRST to outline taking math tools typically used to analyze computer algorithms and applying them to human behavior analysis? Whereas you are proposing to write a paper about something “eerily similar”, so will get it published in a more specialist journal and can expect the article to have less impact?
The novelty-“impact”(citation count) correlation is well-known in science, and arises because subsequent researchers working on similar problems always want to reference the ‘source’ of an idea, not one of the upmteen subsequent researchers who have walked down the same well-trodden research path.
Of course, being the first with a novel idea that has very limited applicability also won’t get you published Science or Nature. So the formula is simply impact = novelty x widespread applicability.
First time poster here, I found you via a link from Wandering Scientist. I know a few young superstars very similar to Erez. (I work in an applied physics field.)
One thing that comes from excellent academic breeding is fearlessness; 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 confidence is extremely important, not only in identifying topics for papers, but in persevering through the revisions or rejections.
As someone who worked for an advisor with an excellent technical reputation but little glossy magazine experience, I can tell you there is a definite barrier I feel when contemplating submissions to Nature or Nature Progeny. This “Is it really Nature worthy?” that I constantly ask myself (and to which I usually answer “No” and submit to a solid society journal instead) is not what some of my higher-impact colleagues do. They just go for it.
so happy i found your blog before going to college, this is really helpful . Thaks a lot Cal!
I really agree with the following:
things like “impact” seem to be, to me, a skill that humanities based people are much better at – it either comes naturally or with practice, but it seems to be something that scientists find a lot harder to do
And would add that, as a “humanities based person” myself, I would say that people who maximize “impact” are people who think about psychology and sociology, and consider *what people need to know on a societal and personal level in order to advance the overall goals of our civilization.* Frequently, scientists pursue knowledge for its own sake, as opposed to thinking about what people might actually want or need to know in order to improve their own lives. For example, a research paper in public health that cites a new way to reduce IV line infections dramatically and at low cost is going to be cited a lot because people find it useful and applicable to saving lives, while a public health paper that talks about a new, complicated, fascinating, but unrealistically expensive way to do the same thing might not get cited a lot because it’s not something people can actually use.
Basically, I feel that the word “impactful” essentially means, “bringing us closer to our goals as a species.” And to know that, we have to know what goals our species has, which can include things like, 1)understanding why we are the way we are 2)saving lives that would otherwise have been lost. 3)advancing technology in a way that makes our lives easier. If research doesn’t support one of these three goals, I doubt it could ever be considered ‘impactful.’ Just a theory…
An interesting theory.
I wouldn’t agree. There are plenty of highly recognized, high-impact publications in theoretical math and CS and physics (among other fields) that gain their authors a great deal of recognition for being an important technical contribution, but at a fundamental level won’t advance any of those three goals. It’s (in my opinion) one of the problems with cutting-edge science.
Our human drive to take part in the conversation around us makes students in great departments discover great ways to frame questions. That drive also explains our taking part in this conversation right here on Cal’s blog. It is the moving force behind the success of St. John’s College, where the students are in conversation with great minds from Homer onwards. That is why St. John’s fits Cal’s description of a joyful community of learning.
I really liked the post.
I’ve also noticed really good people do seem to focus on impact vs impactiness (channeling my inner Colbert)
For instance (thinking out loud):
person of impact – seems to stay take almost a baby steps approach to everything ..and builds a thing or even a new skill that can be shown to someone else. Eventually the accumulation is something much larger …almost magical and amazing the the audience.
person of impactiness – seems to do a lot of work, stays busy, closure to an activity is not quite imagined or never really in sight . Then positions the activities and trajectory of an effort as success (or failure).
When I look back at my own mixed bag I see myself in both modes 🙂
Someone might have said this already, but you should talk to more people in these fields to understand what’s going on. The cultural context here is really, really important. Eric Lander and Martin Nowak are powerful. I knew Erez before he was a grad student, and he was extremely confident then. Confidence and boldness pay off enormously in academia–and with powerful mentors, one can go “critical” as Erez has. It’s not undeserved (he’s extremely talented!), but the social momentum ratchets things up an order of magnitude.
After quickly skimming the comments: What GMP said. I’ve two glossy-mag articles, and each required audacity from lab members that I’m not sure I could’ve summoned on my own.
does Erez have a mission statement that reads: apply X to interesting new things? 😉
Cal, your last paragraph really struck a chord with me. As a graduate student in engineering I am always wondering why certain people/labs have it and and others do not. Culture defines the expectations and the quality of work. Without the “correct” culture smart/hard working individuals sink and fail in academia. I find it hard to assemble the people with that kind of culture, they are just too rare and hard to encounter.
If you allow me, all best wishes for the ladies! March is their month.
A little late to the party here, but it’s been my experience that the scientists that can consistently publish “high-impact” papers have a very broad knowledge of their field and beyond. Understanding the context of what people know and don’t know on a large scale is difficult, but once you do, it allows you to pick problems so that people will pay attention to you when you solve them (and just as importantly, it will help you write the paper so it is framed so many different kinds of people can appreciate it).
It is one thing to start with some mathematical tools and look for problems to apply them to. It is another thing to start with an important question and to burrow deeper until you find the right tool to use.