Ten simple rules...

Here are a couple of useful articles, courtesy of PLoS Computation Biology:

Ten simple rules for getting grants

Ten simple rules for getting published

Both getting grants and getting published can easily get over-complicated, and I personally find it very useful to try to keep things as simple as possible.

An algorithm for selecting research projects

I spend a lot of time thinking about my research projects.  I revise and tweak the ones I'm working on, but I especially spend time planning my possible future projects, working out which ones I should most prioritise.

This is important.  Choosing which projects to work on will fundamentally affect your research career, and given that a project might last months or years, spending hours or days making good choices seems pretty sensible.

I once read a suggested approach that I've come to realise has a lot of merit.  Annoyingly, I can't track down the original reference (I think it may have been by Daniel Lemire or Study Hacks; even if not, you should go and read those blogs as they're very good).  But the idea is this:

Identify your two best/most valuable pieces of research.
Your new project should better at least one of these.

That's it.

It's a really simple approach choosing new projects, and it's kind of obvious that this should lead to good projects (provided your assessment of value is reasonable).  But there's actually an interesting alternative way of describing it.

It's a hill-climbing algorithm for optimising the scientific value of your new projects over time.

Think about it.  We can imagine that there is some abstract quantity, "value", associated with each of the research projects that we work on.  Different people may disagree on the precise value of any given project (and even the definition), but overall we would like to be working on progressively more valuable projects.  By using the above algorithm as a criterion for deciding which projects to work on, we are aiming to always increase the value of our two best pieces of research (by progressively replacing each one with something better).

Why not the best one or three projects?  Well of course, it should still work if you change the number.  Two is probably a good number, as having a couple of headline grabbing projects is useful for writing grants, giving talks and the like.

It occurs to me that it would be very easy to always use the same scale for assessing how good/bad a potential project will be.  But by using the Top-Two algorithm, you're always pushing to do more and more valuable work.  And this seems like a thoroughly good idea to me.

a 'Pool-of-Memes' approach to research

I tend to spend a fair amount of time thinking about how best to go about research. My rationale is that simply working harder isn't scalable - you can't work more than 24 hours a day (and indeed only a lot less than that in a sustainable way). Therefore to be a better scientific researcher, I need to find ways to improve my approach to research.

Study Hack's excellent article on his research system got me thinking about how I'd describe my own system of research. I think the phrase "pool of memes" fits pretty well.

I try to fill my mind with as many interesting/relevant ideas and concepts as possible. This means both being well read in my own subjects, and also hunting out other subject areas that might add something. For example, for the last year or two I've been becoming increasingly interested in computer science. I've found my most productive phases correspond to learning a new set of relevant ideas.

To this pool, I also try to add clear ideas about what questions are important in various areas of research.

Then I just sort of let all these ideas mull. I might think about something in an idle moment at the gym, or I might head to a coffee shop with my log book and tinker with some thoughts.

What I get from this is a list of possible projects on which to work. This list tends to be pretty organic and it evolves over time. I rank the list in terms of how good/important I think they are. And then I try out the top ones.

What I've not had previously, but what I'm just starting to add, is a stage like Study Hack's "small bets". The idea here is to try out the possible good projects for a month or so, with the aim of producing some concrete evidence as to whether or not to take the any further. I'm not very comfortable on a personal level with the idea of discarding projects like this (I don't like the waste), but objectively it makes a great deal of sense, so I may just need to get over myself

:-)

As much as anything, this approach works well for me because I really enjoy learning new things, so giving myself the justification for doing that during work time is nice :-)

Changing disciplines

You don't have to work in the same research discipline for your entire career. Indeed, at least some drift is probably the norm, if only because most problems don't warrant 40 years of attention. But researchers tend to be very focused and dedicated to their subject, spending many thousands of hours exploring it and communicating their findings to the world. They become known for it - "Susan the cosmologist", "Steve the mouse guy".

But it doesn't have to be that way. You could change disciplines.

There are a number of pros to this. You learn a lot of new things when you change discipline. Not just the facts and figures of the new subject (although there are many of these), but also you find out how people in that discipline approach scientific research. How do they collaborate? What are their conferences like? How do they write their papers? All these things can be surprisingly different from subject to subject, and you can learn a lot by seeing different ways of making these things work.

All this new knowledge is stimulating. Not only is this a great experience for the knowledge-hungry academic, but it's a great way of generating new ideas. Perhaps there are problems in the new subject that are much more tractable using the old subject's mindset. Or perhaps you had a general problem you'd been thinking about, and an idea known about in the new subject gives you a "Eureka!" moment.

You can also act as a vector for good ideas flowing between subjects. This is why interdisciplinary work can be so valuable. When the good ideas of two different disciplines mix, sometimes you get important new discoveries. Being the cause of this is obviously a Good Thing.

Sometimes, moving allows you to find a better niche for yourself. There are all sorts of reasons that determine how well you 'fit' in any job and research is no different. Do the day-to-day tasks suit your temperament? Are you happy working on decade-long projects, or is six months a better timescale for you? How well do you gel with the culture in a given discipline? How well does your particular set of research interests fit into a particular discipline.

Depending on the specifics of the change, the practicalities of funding might become easier. One good reason for moving disciplines is to move from one where there's little funding to another that has much better support. I don't think this should ever be the primary reason for moving (and I don't think most scientists do research for the money!), but all other things being equal, wouldn't it be nice to not have to worry quite so much about where the funding is going to come from?

It can also be the case that changing disciplines freshens things up for you. Working on the same small set of problems for a decade or more can get quite same-ish, so moving on to a new set of challenges can open a wellspring of enthusiasm.

A well-judged change of discipline can be a great move, but of course it's not without downsides. It take a big commitment of time and effort, because there will be many new things you need to learn and you'll likely be moving jobs at the same time, so there will be the normal upheavals that this implies (you might even be moving house or moving to a different country). And you'll stay junior in your career for longer. In your new subject, you'll be a rookie even if you bring a lot of relevant skills, plus you won't have a network of contacts and collaborators yet, so these will need building. And your publication list in the new subject will need time to develop, before you can start applying for fellowships etc. None of this is to say that change is bad; simply that there are costs associated with a change this big.

In conclusion, there's a lot to consider if you're thinking about changing disciplines. And rightly so - it's a huge commitment. But if you make the right change, there can be a lot of benefit. And here's one more thought: Maybe the modern scientist should always be looking to diversify?

Why do you work on the science you work on?

What was the decision-making process? How did you make the choice?

Early in my research career, I discovered that I loved working with statistical inference and building the software to do it. I had chosen my PhD because I knew I was interested in astrophysics and I was offered a place at a good department to work on observational cosmology (which I found and still find fascinating). Gradually over the years my horizons have broadened, to the point where I now work mainly on medical and biological data. But the key point is that I'm using statistical inference and programming to do science.

I certainly didn't see this path coming - it evolved.

I suspect this is true for a lot (maybe even most) scientists. Maybe the subject was something that interested them during their degree. Or perhaps it's what they're trained for, given the choice of undergraduate degree they made. That's sobering - the choice you made aged 17 can define your entire career. Anyone else want a 17-year-old picking your career for you? Thought not...

My guess is that many people aren't sure what to do next. They enjoyed their undergraduate degree and therefore (quite reasonably) decided to do a masters in the same or a similar subject. That also turned out to be interesting and, still lacking inspiration as to a career direction, a PhD beckoned (perhaps they were even offered a place by their Msc supervisor, making it an easy option). Suddenly, they're in their mid-twenties, have a doctorate and almost a decade of training in an academic subject. Sounds like a good basis for academia, so off they trot.

Some people want to stay at the same university and this affects their choice of subject (I'll admit to this a little bit). Given a choice of several interesting topics, they take the one that also allows them to stay where they want to be.

Perhaps the subject in question was/is an up-and-coming area with the prospect of lots of interesting science to work on and important problems to tackle. This seems like a not unreasonable consideration.

And of course some people have a burning passion for the subject (something which strikes me as a very good reason indeed!).

As you progress through your career, you'll learn more about what your chosen subject is really like. Are the scientific challenges important? Is it well-funded? What do you really enjoy doing on a day-to-day basis? And do you try to change things in response to this knowledge? What if after five years in one field, you realise that another field might suit you better for whatever reason. Would you change?

I once read a suggestion that in life you shouldn't pick a good destination, but rather focus on a good direction in which to go. The point is that as you live and experience life and learn from it, you'll be better able to make future decisions about where to go. If you pick your path through life now and stick to it, you'll have to turn down all those unexpected opportunities that occur tomorrow. And the You of 5 years time is probably a better judge of where you should be going at that point than you are right now; so why not defer to your (future) superior judgement?

And the point of all this? Think about why you work on the things you work on. And be willing to be flexible. Even if your current plan is a good one, you might happen upon an even better one tomorrow!

Why start a research blog?

As I've just started a research blog, I thought "Why do this?" was a sensible question to contemplate. (actually, I thought about it before I started, which seemed even more sensible...)

Sharing some thoughts...
Sometimes the best way to learn or come up with good new ideas is to talk to a fellow scientist. This is why chats over coffee and meeting up a conferences is so important (and why a few glasses of wine at a conference dinner can lead to valuable conversations). This works because of the ideas that are being shared.

There's no reason why talking should be the only medium through which to communicate in this way. And while a blog is less two-way (although please feel free to leave a comment!), it has the great advantage of being able to potentially reach a huge audience. It's difficult to have a conversation with more than a few people, and even a lecture/conference talk is unlikely to have an audience of more than a couple of hundred people (web-casts excepted). But there's nothing to stop thousands upon thousands of people reading a blog post!

Knowing your own mind
There's also a second benefit to writing one's ideas down in a blog post. It helps to clarify them. Writing something for an audience forces you to thing about what you're writing, to work it into a form that will be understandable by the reader, even to challenge your own assumptions. This can develop your own ideas and trains-of-thought in ways that simply thinking about them won't manage.

Returning the favour
Another very important reason is that I've found other people's research blogs very helpful in learning more about how to be a scientist (see myblogroll for some excellent examples). Not every blog will be useful for every reader, but it strikes me that if every researcher kept a blog where they posted their thoughts, observations and experiences, collectively that would form a great body of knowledge for other people to explore.

In conclusion...
There are several great reasons why a scientific researcher should consider keeping a research blog. And there may well be others that I've not thought of yet, but that will occur as I post on more topics. Which is itself an illustration of why research blogging is a good idea :-)