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30/52 How to evaluate a translational research proposal

Updated: Aug 30, 2023

Bettina Ryll


With patient engagement becoming standard practice, patient advocates increasingly find themselves tasked with reviewing not only clinical but also translational research proposals. While translational research might seem far away from a patient's reality, there are two main reasons why we as patient advocates should take translational research seriously:

  • without translation today, there will be nothing to implement tomorrow

  • errors made and time lost in translation cannot be recovered at a later point in time.

These are the major issues I have picked up in translational research proposals- concerning the research question, the experimental design, the anticipation of scale and project delivery- that if gone wrong will hurt patients:


1- the research question does not address the real problem (but claims the funding as if it did). This is fundamental- if the original question is not posed correctly, anything built on it is on shaky grounds- and also, most often overlooked. The research question determines the experimental design and with that, effort required and cost. So often, what we see is rather that the question gets adjusted to what is readily available in terms of experimental design. An example would be the approach to studying acquired resistance to therapy in Melanoma- by now, we have an entire phonebook of *possible* mechanisms of resistance but the real challenge was never to have a phonebook of possibilities but rather to understand- and overcome- the clinical presentation of therapy resistance. While this might seem like splitting hairs- the experimental and conceptual approach- as well as its meaningfulness for patients- is fundamentally different: one just produces papers, the other patient outcomes.


Even with a correctly posed research question, research proposals often fall short in their design, the following points listing some of the most common culprits.


2- wrong method or wrong model to start with. Every method and model has advantages and limitations, so the choice should be motivated and limitations accounted for.


3- tiny numbers, selection bias, undue extrapolation. Samples chosen rather for curiosity value than clinical representativeness. Just because it's interesting doesn't mean it's clinically meaningful.


4- lack of clinical validation of models. Extensive work in artificial model systems like cell cultures or animal models- and no or limited validation on clinical samples. That might show it was all an artefact of the model system- which is why you should insist on it.


5- exploration, no validation, an absolute classic for biomarkers. Produces nothing but papers and no value for patients. Insisting on a pre-planned validation strategy for biomarkers is therefore good practice.


Translational research is ultimately about getting research findings into routine healthcare- and that means a need for scale. Scale at the scale of healthcare usually means commercial services or products and things that tend to go wrong here are


6- no commercialisation strategy, ignorance of regulatory requirements - e.g. IVDR- and no understanding of the needs of clinical validation in e.g. a clinical trial for reimbursement by national healthcare systems. It's not about one partner having to have it all- but rather to have the right expertise on board or how to access it.


And last but not least, the best idea is nothing without delivery, so something to look for would be


7- do the time-lines fit? A classic would be xenograft mice 'to test response to therapy'- if you then look at the timelines, you realise that most patients will be dead before anyone will have any answer from any xenograft experiment. And if carefully going through the 'success' stories- these were patients with extremely slow-progressing tumours....


8- all complex consortia promise synergies but yet again, time-lines are a good tell-sign. If work packages are supposed to build on each other but the results of the first are due by the end of the project you know....it's not going to happen. 'Hit&Run' consortia- everyone gets their budget and does whatever they like- also fail to deliver on synergies, so it's worth looking at how different parts are supposed to contribute to the overall intended success.


A common request for patient involvement is for it to be inclusive. It should be clear from the points above that evaluation at this level requires not only expertise in the relevant scientific domain but also adjacent fields, like understanding of the regulatory context, business development, Health Technology Assessment (HTA) and how reimbursement decisions are made as well as scientific project management (and probably some more).


Apart from the fact that the inclusiveness argument is frequently used to silence undesired criticism, 'if not everyone can comment, no one is allowed to comment', mistakes in these areas *will* hurt patients, independently of whether the evaluating party understands them or not. The ask to us as patient advocates should therefore be clear: it is on us to assemble the necessary capacity in our communities to protect those very communities. Disease cuts across society- we often even have the right expertise right under our noses but don't notice let alone leverage it. It is unlikely one single person will have it all- but a group of people will. Preparation helps, too. Spending time on for example, diagnostics development and in particular now, IVDR, is time well-invested.


Our goal should be the best possible research with the fastest possible translation at equitable scale as that will have the highest impact for patients. Is reviewing translational research proposals going to be the most effective way to get there? Probably not, but as the saying goes....'to herd cats, move the fodder'. Gender balance, communication and outreach, impact assessments and patient engagement are all areas that are becoming more consistently and meaningfully addressed since funders demand it. Reviewing proposals and based on that making suggestions which common culprits- like lack of validation- should become compulsory to address in the next grant round would be the next step up.


And then, no one prevents anyone from using that knowledge to for example make sure that research consortia, that work on topics central to the interests of our communities, are successful, right?


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