“The intellectual mountaineer makes false starts, gets stuck, gets into blind alleys and cul-de-sacs, finds himself in untenable positions, has to backtrack and start again. Thus slowly and painfully, with innumerable errors and corrections, he makes his zigzag path up the mountain.” Helmholtz
At the end of 2024, I retired and reflected on my career, and presented some lessons about research and research strategy – mostly those I wished I’d known earlier. That retirement presentation was redone as a short video (18 minutes) but below a summary of the five lessons.
Research is like a journey into uncharted territory: you should to have an overall picture of where you’re going (ideally focused on a “big problem”), but then take the journey one step at the time (Picture). So setting out below are some suggested principles for a successful journey.
1. Focus on a big problem, but take small steps.
Research strategy is most helpful when it is focused on a big problem rather than research that seems interesting and do-able. However, the big problem will usually not be soluble or reachable in one step. In healthcare that “big problem” is best expressed in terms of patient outcomes: why is this a problem for patients health?
Finding the big problem is not necessarily easy. Indeed, “problem finding” is itself a skill. The ability to identify something that others do not necessarily see, or assume is insoluble. For example, Farber’s determination to treat leukaemia; Clark’s development of a bionic ear; Wennberg’s concern about variations in medical practice; and Montori’s concern with the “burden of treatment” we place on patient’s. (Note: Many other were involved and even preceded these folk, but I’ve given the names as a guide to picking up the threads of the story).
A common error is to define a problem in terms of a preferred solution. For example, we might be concerned about ‘the poor training of medical students in evidence based medicine’. While that is a problem, it is better focus on the fact that many patients miss out on effective treatments but undergo ineffective treatments. Training students in EBM is just one of many possible solutions to that patient problem; but framing in terms of the “training” solution rules out many other options.
2. Document and understand the problem – preferably with the help of end users.
To make progress towards the distant goal – of solving the problem – will usually require a better understanding of the nature of our problem. Making good maps of the territory we plan to cover if crucial: think of John Snow’s mappings of the cholera cases in London. The maps will necessarily be incomplete – the map is not the territory – so we may need several maps for different perspectives. To stretch the metaphor, we may have a map for height above sea level and another map for the waterways.
Example. When we were trying to understand the expansions in the definitions of diseases, we needed to understand: who changed the definitions? how did they change them? and what information was used to based changes on? That was an important first step before working on solutions to the definitions problem.
3. Learn from similar research journeys and previous attempts
You are not the first researcher, and others will have insight into similar research processes. I have learnt considerably from reading the biographies of researchers such as Stanley Milgram (the obedience experiments), Graeme Clark (bionic ear), Stephen Jay Gould (punctuated equilibrium in evolution), Edison and others.
It’s useful to briefly outline your own ideas first before doing a literature review. Most of your own ideas will have been thought off before, but some may not and reading first can close your mind to other options. But don’t spend too long on this, and always do a thorough review.
4. Build better tools – but keep in mind the purpose
When exploring new territory, keep in mind that progress may be speeded up with some purpose-built tools. So don’t persist in digging a ditch with a spoon when you might invent the shovel (or even a backhoe!). But then work with good toolmakers in devising those tools. The process works best when the explorer and toolmaker work together to towards a common understanding of what is needed. Explorer will usually be poor at designing and building the best tools; but tool makers can be easily distracted by new ideas that don’t help solve the problem.
5. Keep your focus on the big problem, but be alert to interesting accidents
Many of the biggest breakthroughs in medicine have occurred when a researcher has actually been seeking something else. For example Fleming noticing the lack of growth around the (penicillin) mould his Petri dishes; Ridley noticing that the plastic embedded in a patients eye caused no reaction – enabling the intraocular lens; or Koller noticing that cocaine numbed the tongue, triggering the idea of local anaesthetics.
The above is intended to give a big picture of the research process can take years or decades the big problem accessing card during this process but along the way the research will publish many of the small steps and illustration is Graeme Clark’s invention of the bionic ear (see box) which took around 12 years from idea to the first (impractical) prototype; and another 5 years until clinical trials.
I’d be interested to hear the lessons of others, so please post in the Comments section.
Healthy Evidence 
Could a driver diagram, borrowed from the QI world, apply to #2? Or is a different or less formal process likely to be more fruitful?
Good idea Jessica – using QI tools such as “7 whys” or fishbone diagram might help with causes/solutions. But often a first step is just more observation and perspectives on the problem.
Great post, few questions: As you know, women have been underrepresented and understudied in much of the medical research that informs medical practice today. 1. Is it possible to go back to previous clinical studies where men & women were enrolled and apply missing sex-based analysis to the data to glean new insights? 2. In your opinion, would these new conclusions be strong & valid enough to (justify the effort) and shed light on new pathways forward in women’s health? Thank you.
Dear Claudia – a good idea but sometimes not possible, and even when possible, it is lots of work. In general you would need to have Individual Patient Data Meta-analysis to have the statistical power to look at subgroups such as female vs male. But those are much more work (x 10 at least) and require the cooperation of the primary study’s authors.