Most weak ERC proposals are not weak because the researcher lacks technical competence. The more common problem is that the scientific judgement remains hidden behind detail.
The proposal may contain excellent methods, a strong CV and an important topic, yet still leave the reviewer uncertain about the central question, the intellectual leap or the potential change to the field.
These are the mistakes I would look for first.
1. Treating ambition as a specification increase
A proposal can promise better sensitivity, higher resolution, faster computation or improved efficiency without being scientifically transformative.
Specifications are outcomes. The deeper ERC question is what new understanding or capability the improved specification makes possible.
Instead of:
We will improve resolution by 30%.
Ask:
Which scientific regime becomes observable if this limit is crossed, and what question can then be answered for the first time?
Ambition lives in the scientific consequence.
2. Starting from methods instead of the unknown
Researchers naturally think in experiments and techniques because that is how daily work happens.
An ERC proposal benefits from reversing the order.
Start with:
- what the field does not know;
- why that unknown matters;
- what hypothesis or concept could resolve it;
- what evidence is needed.
Methods should enter after the scientific decision is clear.
3. Having several interesting objectives but no central question
A proposal can contain four excellent objectives and still feel fragmented.
If the objectives do not resolve one coherent scientific uncertainty, the programme can look like a portfolio of projects.
Try to write one sentence that explains why all objectives have to exist in the same grant.
If that sentence is difficult, the intellectual spine may still be missing.
4. Making the hypothesis effectively impossible to falsify
A proposal sometimes claims to be high risk while every outcome is framed as confirmation.
That weakens the scientific logic.
A useful hypothesis should create the possibility of being wrong.
The important design question is not how to avoid that possibility. It is how the programme remains scientifically productive if the preferred answer is wrong.
5. Treating failure only as project-management risk
A standard risk table may say:
If method A fails, use method B.
That can be operationally useful. It does not explain the scientific value of unexpected results.
A stronger proposal also asks:
- What if the effect is absent?
- What if the relationship reverses?
- What if two mechanisms coexist?
- What if the transition occurs in a different regime?
Each outcome can redirect the research without destroying the programme.
6. Writing Part I like a methods paper
Part I has five pages.
Using too much of that space on technical implementation can make the proposal scientifically smaller because the reader never sees the full vision.
Part I should establish:
- importance;
- current limitation;
- question;
- new idea;
- objectives;
- research strategy;
- potential change to the field.
Detailed implementation belongs primarily in Part II.
7. Explaining importance for too long
The opposite mistake also occurs.
Some proposals spend several pages proving that a broad field is important.
A reviewer rarely needs a long argument that cancer, climate, quantum technologies, AI or energy matter.
The valuable question is why this unresolved scientific problem matters within that field.
Use enough context to establish significance, then move to the intellectual gap.
8. Using figures decoratively
A figure in Part I consumes scarce space.
It should clarify the scientific argument.
Avoid graphics whose main message is that the project has four work packages, several arrows and a five-year timeline.
Use figures to show:
- a conceptual gap;
- competing explanations;
- the regime the project opens;
- the hypothesis and outcomes;
- the field-level shift.
9. Showing so much preliminary evidence that the question looks answered
Preliminary results can establish plausibility and access.
Too much evidence can create a different problem: the reviewer may wonder why a five-year ERC grant is needed if the core claim already appears demonstrated.
The ideal evidence says:
We know enough to justify asking the question. We do not yet know the answer.
10. Treating the team as a staffing table
An ERC Starting Grant can build a research group.
The team should reflect the scientific architecture.
A useful team design explains:
- why a postdoc needs senior autonomy;
- which objective requires doctoral depth;
- what the PI personally leads;
- which expertise is collaborative rather than internal;
- how the group remains coherent.
The question is not simply how many people can fit in the budget.
11. Failing to demonstrate scientific independence
A strong publication record does not automatically communicate independence.
The proposal should make it clear what is intellectually new relative to the PI's previous environment.
Ask:
- Is this my question?
- Is the programme recognisably mine?
- Does it extend beyond the trajectory of my former supervisor or group?
- Am I now setting the scientific direction rather than contributing to someone else's?
12. Choosing the panel by department name
A proposal may sit between fields.
Choose the panel most likely to understand the central breakthrough, not the one that matches the PI's institutional label.
The central question should guide panel choice.
13. Hiding the payoff until the conclusion
The reviewer should not need to reach page five to understand why the project matters.
State the potential scientific change early.
Precision keeps that ambition credible.
There is a large difference between:
This project will revolutionise quantum science.
and:
If mechanism X is confirmed, the accepted sensitivity limit becomes contingent rather than fundamental, opening a new class of measurements in regime Y.
The second is ambitious and testable.
14. Trying to remove all uncertainty
A proposal can become less convincing when it promises that every part is already under control.
A EUR 1.5 million frontier-research grant should contain real scientific uncertainty.
The objective is to control the execution well enough that the uncertainty can be explored rigorously.
15. Editing for polish before solving the science
A perfectly written proposal cannot compensate for an underdeveloped scientific question.
I would resolve the following before spending heavily on wording:
- central question;
- scientific importance;
- hypothesis or proposition;
- outcome space;
- objectives;
- PI-project fit.
Once those are stable, editing becomes much more valuable.
A useful final diagnostic
I would ask a researcher to answer these questions without opening the proposal:
- What is the question?
- Why does it matter?
- What is genuinely unknown?
- What might fail scientifically?
- What would still be learned?
- What changes if the strongest outcome is achieved?
- Why is this programme yours to lead?
If the answers are difficult, the proposal likely still has a structural problem rather than a wording problem.