Planning in research: from long-term strategy to a single experiment. Part 1: Strategy

Good planning is absolutely essential in research. It is what makes a difference between a competent scientist who does decent work, and an excellent one who really pushes the envelope. People with poor planning skills will waste tons of time on futile projects and so will not be able to focus on what really matters. While good planning is something that comes naturally with experience, I think it’s useful to have a framework you can refer to at any career stage. The framework I use can be divided into three levels: Strategic planning, tactical planning, and planning of single experiments. Single experiment planning was roughly summed up in my post about “the gory details“, and I will talk about tactical planning in my next post, so let’s get right into strategic planning.

This is where you decide on what projects to focus on and which ones to drop. This is also where you sketch out the tree of life of your project and decide on experimental priorities. On that level, you should put yourself in the shoes of a hypothetical critical reviewer of your project. When reviewers judge grant applications, what do they look at? In short, they will evaluate your project on its potential impact, its feasibility, and the strength of preliminary data that support the direction you want to go in. Even if you are not planning to submit a grant application right away, you should try to be your own reviewer.

1. Impact

Ask yourself the following question: if my hypothesis turns out to be correct, how important will that be? Can you imagine a scientist from outside your discipline reading your paper and saying – wow, that’s really interesting! Perhaps it’s not quite CNS material, but it will still make ripples in your discipline, or your specific sub-field? Or maybe it’s just interesting to you and a couple of people in your lab and no one else? If the potential impact of your project is limited, than maybe you should take some time and come up with a better way of spending your time and effort.

Judging impact is a real art and I think it really comes with experience. You need to read outside of your sub-discipline to figure out what kind of studies tend to get the spotlight and what kind slowly die in the zero-citations limbo. If you have doubts on whether your project has potential, ask someone for feedback. Preferably someone from outside your discipline. They don’t need to know all the details – just a 5 minute summary of your planned project should be enough for a seasoned scientist to evaluate it in terms of impact.

An important aspect of impact is novelty. Make sure that you have scoured the darkest corners of pubmed and google scholar for prior publications on the same topic. It’s not unusual to have worked on a project for six months or more, only to discover that the finding had been published five years earlier. Citations patterns in papers tend to sometimes “isolate” some findings from some other fields, and you end up reinventing the wheel. If you want to judge novelty, you can also ask for feedback, but your expert should be someone in the field rather than outside of it.

2. Feasibility

There is often an inverse correlation between impact/novelty and feasibility. After all, if it was easy to do a certain high-impact study, someone would have done it already. There are in fact two aspects of feasibility: global and local. Projects that have low global feasibility are just hard in principle – there may be biological limitations (e.g. low abundance of whatever you want to study) or technical limitations (e.g. resolution in microscopy or sensitivity in a mass spectrometer) that nobody in the scientific community has been able to overcome. Projects that are globally feasible, but have low local feasibility are the ones that could be executed by a number of researchers, but you are just not one of them. You lack the expertise or the instruments or the funds to do them.

3. Preliminary data

It is really hard to objectively look at your data without interpreting it from the point of view of your favorite hypothesis. Once a hypothesis pops into your mind, all new data is massaged inside your brain for as long as it takes for them to support the hypothesis. Especially when the new data point in a much more mundane and less exciting direction, we tend to reject what’s in front of our eyes and instead find all kinds of way why the new data may be somehow “wrong”. Actually, this way of thinking is not always counterproductive. Data always has limitations, and if the evidence that made you think of the hypothesis in the first place is really strong and does not allow for alternative interpretations, then by all means, work on the technical details some more. However, if everything conspires to disprove your hypothesis, it may be a good time to talk to a disinterested labmate or colleague and discuss alternative hypotheses.

So how should you decide on what project to work on? It will depend a bit on your priorities. If you are going for a Nature paper, then pick a project with very high impact and perhaps low feasibility. If the low feasibility is local, you can always find a collaborator who will help you out. If you need a paper yesterday because the funding agency and your dean are on your back for lack of productivity, then go for a highly feasible but maybe lower impact study. In all cases, make sure that your preliminary data is solid before going too much in depth. Focus on the skeleton first – your preliminary data should be pure skeleton, no meat. And if your favorite project just isn’t coming together on either front, be it impact, feasibility, or preliminary data, then drop it like it’s hot. There are hundreds of interesting research questions that you are well qualified to work on – don’t waste your time with the trivial ones.

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