When writing an ERC proposal, researchers are aware that they are supposed to be promising to make a big difference, that the objectives when reached are supposed to break new ground and open new frontiers and horizons etc.: this is all abundantly clear from the ERC supporting documentation.

In a large number of the  400+  ERC proposals that I have reviewed over the years a similar idea crops up as a concluding statement in the section on objectives or impacts as the ultimate statement of big differences to be made – the paradigm shift.  And in looking at this idea I’ll move on to the next of the mind maps based on the findings from my review of ERC proposals and begin to work round this group of issues that are still common in a range of texts but are a bit more complex in their nature.

‘Once this or that objective has been reached and all these activities completed and the results obtained I will have made a paradigm shift’, or similar formulations of the idea are quite common. Of course, it is difficult to describe in concrete detail exactly what the project objectives are and what difference they will make when they are reached – this is a big challenge and very time consuming to do and elegantly stated objectives are the test of a really well planned and written proposal. This can only be done successfully and persuasively if the state-of-the-art discussion is done at a fine enough level of resolution to convincingly point out the gaps in completed and ongoing work and if the impacts of reaching the objectives are big enough to warrant the investment against the risk inherent in all research: it is tough to do, both in the conception and in the presentation.

So, what I see fairly often are less-than-perfectly crafted objectives not well articulated with the issues in the state-of-the-art and unlikely to drive major change in the field and appended to this package of argumentation that packs a less than powerful punch is the assertion ‘and this will bring about a paradigm shift in the field’ – it is a cliché and can’t be used to mask a lack of precise analysis and description and it is pointless to try to use it in this way. And even as the culminating claim of a very well worked out proposal it is still a cliché and so creates an unnecessary jarring effect because it is an exaggeration and not what you are being asked to do in these programmes which is ‘simply’ to make important steps forward on the state-of-the-art to create sustainable differences that mean something for how the work in this area unfolds in the future.

As with most other things that can be said in a proposal, this in itself won’t lose the game. However, winning is often an accumulation of small victories as the text unfolds and the not making of errors along the way so that the overall effect is positive and there are no negatives that are obvious to the skim reading evaluator: good texts gradually rise to the surface, less good ones slowly sink down like the blobs in a lava lamp – only they don’t come back up again. So, to say you make a paradigm shift is simply leaves a bad impression which might be the straw that breaks the camel’s back when the accumulation of small infelicities can add up to a percentage point which pushes a text below the threshold for funding and renders the whole enterprise of writing fruitless.

The idea of a paradigm shift was first clearly set out by Thomas Kuhn in his book The Structure of Scientific Revolutions and it is back to this notion of revolution and paradigm change through a more or less meandering pathway, that I think proposers are referring. According to Kuhn, a paradigm shift is a revolutionary change that shatters the way that science looks at the world and is driven by different factors and participants over an extended period of time – one understanding of things is replaced by another. It is not the work of a single ERC project to bring one about or even to make a targeted contribution towards one as they cannot be anticipated or worked towards in this way. Paradigms shift when the anomalies in the prevailing worldview trigger the development of a new way of understanding nature. It is never the work of a single project, very rarely the work of a single person and never happens overnight – and the duration of ERC projects certainly count as ‘overnight’ in this context.

I think it is more likely that ERC projects will be working inside of existing paradigms, in what Kuhn calls ‘normal science’ doing the absolutely vital work of pushing the paradigm as far as it can go and, perhaps, slowly helping to reveal through very fine grained work the weaknesses in the existing frameworks for viewing the world.

He identifies, for example, three normal foci for experimental and observational science in the ‘normal science’ mode and ERC very often takes place in one of these. Firstly, using the facts that the current paradigm has shown to be particularly revealing of the nature of things and using them to solve new problems that scientists consider to be worth determining with more precision and in a greater variety of situations. The second class of scientific work inside a current paradigm is using facts to compare directly with predictions from the paradigm theory. Improving the agreement between the theory and observations from nature or finding new areas of agreement present major challenges to the skill and imagination so scientists. The third category of work inside existing paradigms is the most important of all and consists of empirical work mostly interwoven with theoretical work undertaken to articulate the paradigm theory, resolving some remaining uncertainties and allowing solutions to problems which had previously only been pointed at. It seems fair to say that the vast majority of ERC science, of all science in fact, falls, perfectly correctly, under one of these three headings (or the three headings for theoretical work which are basically the same).I

In fact, I would suggest that for many reasons it is strategically sensible to be making claims about significant steps forward and innovations inside the common and shared discourse of the field. It might even be the case that in some respects these three correspond loosely to the categories of ERC projects i.e., StG, CoG and AdG. It might be useful to bear in mind that even at the highest levels of work in ‘normal science’ mostly the new findings will have been predicted but not demonstrated by other theoretical and experimental work: as Kuhn says – “Even the project whose goal is paradigm articulation does not aim at the unexpected novelty”.

We should keep in mind that proposals are, in essence, applications for funding – this is what drives the text and ultimately gives it its character, despite the fact that many scientists tend to forget it along the way. I’d argue that logically we are on firmer ground when we propose challenging work in recognisable fields with likely results and impacts that push that discourse along significantly but which will be recognised by an overwhelming majority of likely readers – this strategy can be put into place and used to scope subjects for proposals at a very early phase of thinking, I propose. The gaps in the state-of-the-art on which the project is built are less grand and less fundamental than the anomalies in the paradigm that might eventually lead to a scientific revolution, although they might be work that is related to them along with the work of many colleagues across the world. The problems in the state-of-the-art at the heart of ERC projects are more modestly, and again correctly, the currently unknown parts of work being done in the normal science mode. The puzzles that ERC projects solve may or may not add up to a contribution to paradigm change, probably a small one, but this cannot be known in advance and can’t be used to sell the project – it needs to be sold but it simply doesn’t work to claim to be about to create a paradigm shift. So, all this to say a small thing – I’d suggest not saying this and not making this claim and I think it constitutes a small negative mark against any text it appears in.

The idea of the ‘new’ and ‘risky’ is, I think, overplayed somewhat in the discussion of ERC programmes in any of the stronger sense that these words might carry with them. In conversation with ERC officers I have heard it said more than once that this emphasis on the new is, in fact, not really operationalised to a very great extent (the new in a strong sense of unprecedented). When money is at stake as it is here it might be wise to consider how challenging it is actually to think new stuff and how much more difficult it would be to fund the search for the new and to err on the side of caution despite the rhetoric. We are mostly trapped here in Meno’s paradox and don’t really need to fight our way out of it to be successful ERC candidates. Kuhn himself argues that as paradigms slowly shift and the understanding of nature changes and these changes accepted “the new fact (that science might throw up) is not quite a scientific fact at all” and so, in the context of science funding programmes, quite a hard thing to sell.

This is not to doubt the likelihood that very major and landmark work and revolutionary discoveries will be done and made under the aegis of the ERC – I am sure that many important breakthroughs have already been made with many more to come. However, researchers are not under pressure to dream up work of this epoch-making magnitude or add the claim that their work is of it, this is a not making a good percentage bet in what is really a pretty feet-on-the-ground set of programmes. Clear objectives to chip away at a part of a big problem in the field, clear statements of why this is important and why it won’t be done in the current research trajectories in the state-of-the-art and some good strong statements of the beneficial differences this will make is ‘all’ that is being asked of the researcher here.