Additional guidance on the preferred format and style of the ‘case for support’

(Sure you wouldn't prefer the short-form 'key questions' first?)

NB. These notes were originally written in the context of the requirements for proposals to the EPSRC Systems Integration Programme. Requirements in that programme were rather special, but much of what is said here is more widely applicable, and proposers may find them helpful more generally.

At risk of being accused of teaching my grandmothers to suck eggs, I offer here some guidance on the way in which proposals might best be presented. You might well be able to do better by not following this guidance: this is just my own preferred format which helps me to get a feel for the strength of the motivation for the work, and to understand the rationale for the approach and the route by which you will affect the world with the results.

However, there is some evidence that those who have followed this guidance have produced proposals which are more clear for work which is better focused. A secondary benefit is that the referees’ task is much easier – which also works to the proposers’ advantage.

This guidance was originally aimed primarily at academics, who have traditionally written the proposals, but we now recommend that an industrial partner writes at least the first draft. They are not hindered by the mind-set of the traditional academic case for support, and what we seek here is much more like the kind of case for support one would expect in industry.

It may be that the nature of your proposed research is that it is not easily cast in this way, in which case you can ignore all of this. These are not formal requirements. But do think - could it be cast this way? Will others doing similar research be able to prepare a better case than you along these lines? Is the reason that you don’t have a good problem statement because you have not got close enough to your industrial partners? Have you really been imaginative about the way in which your results will create a major impact in the world?

Remember, we are looking to make significant breakthroughs in this programme, not incremental technology development. Do think big - not necessarily in terms of project size, but in terms of intellectual advancement and impact. We are looking for vision.

Relation to existing EPSRC Guidance

This present guidance supplements that provided by EPSRC at:

In particular, I am concerned here with Section 6, the subsection within that concerned with the ‘Case for support’, and primarily the 6-page "Part 2: Description of the proposed research and its context".

However, first a brief word on "Part 1: Previous Research Track Record". You may think it churlish of them, given that this is where you say how wonderful you are, but referees often only skim this section, at best. One reason is that it rarely says anything interesting. Often it is straight boiler-plating - a personal or group cv. That is not what is required. This section is intended to establish (rather than assert) your credibility in both technology and the application domain(s). Too often folk go on for far too long about how clever they are - research & publication record, grants received, etc - without achieving this objective.

When you are crossing – or appear to be crossing – into a new domain your proposal may well be sent to referees expert in that domain but unfamiliar with your work. It is then vital to establish your credibility.

Although it is not a formal requirement, I strongly recommend that you include in Part 1 something about the non-academic collaborators. Since your team’s group competence for the task (presumably) depends upon their participation, say so.

With regard to "Part 2: Description of the proposed research and its context" the official guidance suggests a number of headings, such as ‘Programme and methodology’ and ‘Relevance to beneficiaries’. While referees will look for the information which it is suggested in that guidance should be provided, you do not need to follow its structure slavishly: these aspects should be plainly apparent if you follow the approach I offer below. Indeed, with the experience of two calls behind us, I am more confident that those who follow the structure suggested here - or that of the 'key questions' - generally present their case better, are better understood by both referees and members of the prioritization panel, and - other things being equal - ultimately stand a better chance of support.


My first piece of advice is what information you should not give.


Please do not tell us about how industry is continually restructuring, or how important is the maintenance and evolution of corporate knowledge. In other words, please do not regurgitate all the ‘background’ stuff in the call for proposals. We know all this already, else we would not have made the call. And since anybody can write this stuff, it does not help to differentiate those who really understand it from those who do not.

Then ...


One shortish para on the essence of the proposal – e.g. "This is a proposal to investigate whether the XYZ problem can be alleviated by ABC technology".



This should not be in terms of companies needing to manage their knowledge more effectively. That is far too abstract.

What is it that your industrial partners cannot do, or cannot do well enough, which they will, hopefully, be able to do, or do better, as a consequence of your proposed research?

Take your industrial partners’ practical problem in their business which motivates them to work with you. Consider ...

"This proposal is to develop a decision support system for ..."

Compare with ...

"ABC Helicopter Company transports people between the shore and offshore oil rigs: 75% of missions are aborted at a cost of úNNN,000 per annum, with consequential health and safety risks for both those undertaking the missions and those working on the rigs."

These are slightly sanitised real examples of the opening words to a real proposal (in a different programme) before and after ‘sharpening up’.

One way to avoid being too abstract is to be devil’s advocate. The companies want to do something – say shorten time to market to 30% of the present figure, reduce corporate post-merger rationalisation IT system re-work to 10% of present values. (Remember – we are trying not to be incremental.) OK – let them get on and do it. Usually this elicits a protest "But we can’t do that because ...". So - what’s stopping them? What are the ‘becauses’? More particularly, what is stopping them which academic research might unblock? There are your research targets.

Another way is to keep asking, like a little child,"Why?". What casuses you to make that abstract statement? Why are your bosses allowing you to spend time with these academics? Keep digging further and further back: there must be reality back there somewhere.

However, we are not interested in solving just the particular problem. What is the generalisation of that particular problem? It is that general problem which should be the research problem, which we presume you will be tackling.

Please do not confuse addressing a real-world problem with short-termism. The intention is not that our research should simply solve some company’s immediate problem, but that the problem should inspire us to make some insightful intellectual discovery. What we are seeking is a sense of real motivation - passion even - to impel the research.

In the heading of this section you will see that I added "or opportunity". This is not because of the standard management school line about being positive by seeing problems as opportunities, but because, while many projects will be grappling with industrialists’ heartfelt problems, we must be open to the possibility that some projects might deliver results which open up entirely new markets for products or services. It would not be sensible to force proposals for such projects into an inappropriate mould. However, assuming the problem-driven format for now ...


This is what I sometimes call the first premise of the proposal - what you believe to be the underlying technological or organisational cause of the (generalised) business problem. This is the slot into which your research for a generic contribution will fit.


I suggest you preface this with what has been tried so far. This both (i) demonstrates that you are aware of other approaches to the problem going on elsewhere (too frequently this is not apparent), and (ii) enables you to differentiate your own approach.

The line of attack is what I sometimes call the second premise of the proposal - your ‘big idea’ as to how that underlying cause might be attacked. What do you think will solve or ameliorate the problem? What is your ‘angle’. "We believe that our stuff, by fixing something technical or other, will solve/alleviate/ameliorate the organisational/commercial/socio-technical problem".

In a more formal research context the conjunction of the two premises would be the ‘hypothesis’ - "The cause of problem X is Y and Z will help."

Now, sometimes it might be sufficient for a renowned research team to tackle a problem without having a predetermined line of attack, based simply on their reputation for good work in the field. If you think that referees will accept your proposal on this basis, then go ahead - try it. But I wouldn’t bank on it.



What do you intend to find out - and how will you know that you have done so? The ‘objectives’ are better put this way, so one is less likely to fall into the trap of saying that one will make a model, build a demonstrator, or develop a methodology. You build a model, or run a demonstration, in order to find something out. What is it? A model is part of the ‘how’ - not the ‘what’. What are the research questions entailed by what you intend to find out?

Approach? By this I mean the route to answering your research questions - essentially, the plan.

Referees don’t want to be hear at great length why you believe your approach is a good one: they want to know how it differs from other approaches; an indication of why it might work; and most importantly how you intend to determine whether it will deliver the hoped-for benefits.

Again, you might get away with a good team, a clear problem statement, and a well-articulated set of objectives. But again I would not bank on it. Having visionary ideas and ambitious objectives is all very well, but can be easily undermined by unrealistic resourcing and project planning. A professional plan, which at least looks plausible in terms of resources and scheduling to meet the objectives, adds considerably to the credibility of any proposal.

Quality? We are looking, in this programme, for world class research. Now, it could just be that you have, in your lone university department, the world’s best brains for tackling your chosen problem. If not, then where are those best brains? Involve them - maybe as partners, maybe by visiting fellowships, maybe by international workshops, or by what other mechanisms you can devise.



A set of titles of work-packages does not make a plan.

How and where and when will your industrial partners contribute? Or do you intend to take their problem off them at the outset of the project and deliver a solution to them three years later while they just sit around, maybe reading the occasional research report?

After those three years will they simply take that solution off your hands and overnight completely change their way of working? I doubt it. So what will they be doing to support the research, determine whether the results will solve their problem, and prepare to change their practices to accommodate the results???


How will you change the world?

There should be a realistic route to significant eventual exploitation. This is not to say that there should be a product launched on the market immediately following a project. What we seek is real impact of the results on the issues, the participants and the wider community. The results should not be confined to research papers and just a little ‘in house’ exploitation in some of the industrial partners.

We recognize that the results of projects will vary considerably in nature. Some will probably give just understanding. I do not wish to diminish the value of understanding with that "just". However, it can be useful to consider the metaphor of ‘shrink-wrapping’ the research results to hit a large audience. How might this be done?

In some cases, there may actually be a shrink-wrapped software product. In others, a product supplier (not necessarily software) may modify their product line as a consequence of the research. In each of these cases, assuming the suppliers have a significant presence in the world market, then it is relatively easy to see how a major impact might be achieved. Effectively, the big idea is embodied in the product. That is not enough, but it is a good basis for making the case.

It is much more difficult to see how a major impact will be achieved when the research results lead to an understanding of how to do things differently - simplistically, when the innovation is in a process rather than a product. Too frequently, despite claims in the proposal to achieve widespread take-up in, for instance, user-organisations, the results end up giving, at best, a little insight to those directly involved in the research, and few others.

Also, experience has taught us to be highly sceptical of claims that a toolset will be built to underpin some new methodology - let alone that such a toolset will achieve significant uptake. So if the output of your proposed research is of this kind, then do give serious thought to credible dissemination and exploitation. One might work through consultancies, for instance, but then I, for one, would need some convincing that any consultancy would change their way of working on a large scale as a consequence of the research. If the intention is to change the way of working of many smaller companies, without intermediary consultancy, then how will this be achieved? Television? Videos distributed through Business Links? Could they be reached through their supply chains? Trade Associations? Again, think big, think visionary.

Organisations are often built around a presumed process. If research results require a change of process, then how is that to be brought about? Throw a switch overnight? How will organisations, with structures and a web of ongoing activities locked to the present processes, migrate to the new - and maybe even migrate their structures? If the results might imply restructuring of supply-chains then how is this to be brought about?

Remember, we are not (necessarily) seeking commercialism from researchers - just that they give serious consideration to the way their research results will affect the world.



We are talking about significant sums of money for many projects - more than many venture capitalists put into start-up companies. Yet this is not private capital - you are bidding to spend taxpayers’ funds. Do you think your neighbours would be convinced that it would be a good idea to spend their hard-earned income on your project? Would you be convinced if you had to referee the same proposal coming from another team?

Too much to take in? Try the distilled key questions.

  Bob Malcolm, May 1999

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