3 Questions To Make Your Research More Clinically Relevant

Have you ever watched a promising therapeutic compound sail through its preclinical studies, only to fail during human trials? Unfortunately, this happens more often than not.

And the statistics back it up. When industry tried to reproduce landmark preclinical work in one study, they confirmed their preclinical findings only a fraction of the time [1, 2]. Broader reviews have since reported preclinical irreproducibility at a whopping 75–90% [3]. Meanwhile, the journey from lab discovery to routine clinical practice has been estimated at around 17 years [4].

Unfortunately, the preclinical research behind new drugs can be excellent and rigorous, but still not translate to the clinic. Here’s how you can avoid that in your own drug discovery research.

The Lab Optimizes Perfection, The Clinic Optimizes Patient Outcomes

I’ve worked in three places that taught me that a beautifully constructed research question can be irrelevant to human patients. I started in optometry, face-to-face with patients and their unmet needs. I then spent a year conducting research on the crystalline lens and ophthalmic biophysics, where I noticed that many of our experimental questions were disconnected from day-to-day patient care. Now, during my PhD, I work under a clinician on infectious keratitis and medical device development.

Moving between these worlds showed me that clinical relevance is determined the moment you choose your drug target, your model, and your experimental endpoint. In my experience, the most fragile point in the whole drug discovery process is the transition from preclinical work to first-in-man studies. That’s where your science meets real life, and it’s a stage the literature consistently flags as a major point of attrition [5].

Use These 3 Questions to Test Clinical Relevance

In my experience, translational failures tend to have the same cause: an experimental question that did not consider the final patient outcomes. These include:

1. Clinically irrelevant targets: a cell signaling pathway that is important in a cell culture or animal model but plays a minor role in the human disease.
2. Non-representative models: an animal model that does not capture the heterogeneity, comorbidities, and treatment history of human patients. This has been repeatedly identified as a core reason why preclinical findings fail to translate to humans [6].
3. Outcomes that don’t matter to patients: an experimental endpoint that doesn’t correlate with patient outcomes. Remember that statistical significance in the lab and clinical significance for a patient are not the same thing; data can be significant on the bench and mean nothing bedside.

Notice that none of these have to do with rigor; rather, each is an experiment designed without considering the clinical reality. The good news is that “is this question clinically relevant?” is something you can actually test before you run a single experiment. That is exactly what the following three questions will help you figure out.

Question 1: Is this drug target relevant to the real disease?

When thinking about drug targets, most researchers want to focus on a pathway component that is clean and mechanistic, e.g., “Does protein X increase in stimulated cells?” It’s a tidy hypothesis, but may have very little to do with how the disease presents in real life.

A more clinically relevant version of this hypothesis can keep the same target but grounds the question in patient outcomes: “Is protein X elevated in patients with severe keratitis compared with those with mild keratitis?” This question investigates the same protein, but now the answer tells you something about the real disease across a range of clinical presentations.

Question 2: Will this change a clinical decision?

Next, ask not whether a disease mechanism exists, but whether knowing it existed would impact clinical behavior. For example, “Does biomarker Y exist in this tissue?” is a fact. “Can biomarker Y predict treatment response, tell you a patient will heal sooner, or guide a therapy choice beyond the standard antibiotic?” influences a clinical decision.

This is where you should be suspicious of endpoints chosen for their statistical convenience. For example, in a preclinical corneal study, you can measure how long the ulcer takes to heal. That experimental data is relevant to outcomes that would benefit a patient. On the other hand, a change in protein expression alone often doesn’t tell you whether a patient will feel any better in real life.

Question 3: Can this actually be done in the real world?

The last question is around feasibility, and it’s the one researchers often forget. If your method depends on equipment that isn’t available in routine practice (e.g., mass spectrometry), its clinical value may be limited no matter how elegant your results are.

The point of a translational study is to generate actionable knowledge that someone can use in day-to-day patient care. So ask early:

• Can this intervention be implemented realistically?
• Can a patient actually adhere to it?
• Can a health system afford it?

These questions feel deflating at the grant proposal stage, but they can save years of work and thousands of research dollars down the line.

Worked example: Keratitis

Let me show you how these three questions work with an example:

When investigating keratitis in the lab, we tend to assume a single pathogen infecting an animal model, and we measure antimicrobial efficacy or the in vitro minimum inhibitory concentration of the drug. That’s a perfectly rigorous study. But it’s also modeled on a perfect disease that doesn’t exist in the clinic.

Real patients with infectious keratitis are much more complicated. Because the epithelium is open, a patient can have a mixed or superadded infection, not one caused by a single pathogen. They’ve also often used steroids and an assortment of antibiotics prescribed to them before they reach us. And they commonly present at very different stages: the late presenters have worse enzymatic degradation of the cornea and much thinner corneas.

To complicate matters further, some are simply not very compliant with the drops we prescribe, affecting treatment efficacy.

If you run this preclinical study through the prescribed questions, it is flagged by all three:

1. Relevant to the real disease? Not if the disease is usually polymicrobial.
2. Changes a clinical decision? Not if the endpoint is MIC rather than whether the cornea clears.
3. Feasible? Possibly, but you haven’t checked adherence.

So while a drug optimized against a single pathogen in an experimental model can be beautifully effective in the lab, its effects might not be as significant in the clinic. Ideally, you would redesign this experiment before you start.

Because you often can’t count on knowing which pathogen you’re facing in a human patient, you might aim for a treatment that retains efficacy across all the microbes a keratitis patient is likely to carry. Finally, you add endpoints that mean something to clinical outputs, such as corneal clarity and healing time.

Unfortunately, this isn’t easy

If there’s one place to put effort into clinical translation, it’s earlier than you think. When I’ve brought a clinician in late, I’ve paid for it in time and money. However, when I’ve done it early, they’ve caught things I couldn’t have; for example, a preclinical dose we’d never actually give to a patient, a dose that isn’t available, or a target that isn’t stable at the right temperature. In some cases, they have also helped me write the grant proposal itself.

Seeing eye to eye

Clinicians and bench scientists effectively speak two different languages, so a clinician won’t always see why you need a particular experiment or sample. When that happens, I come back with the literature and show the clinician how it connects to the patient or the disease. The alternative is discovering the mismatch after the data is collected, when the funding is granted, and it’s too late to change anything!

Key Takeaways

If you take anything away from this article, remember to:

1. Start with a real clinical problem, not a molecule in a pathway.
2. Choose models that better reflect the disease and its heterogeneity.
3. Define the endpoints clinicians actually use, not just those that are statistically significant.
4. Think about clinical feasibility at the very beginning, i.e., implementability, patient adherence, and whether the health system can afford the result.

What’s hardest about these principles is applying them when the elegant version of the study looks easier to fund than the messy, more clinically relevant version.

But if you’re the kind of scientist who’d rather find the flaw in a study before running it than after publishing it, put these three questions at the top of your next proposal, before a single experiment is designed. It’s the cheapest, highest-leverage review your work will ever get. Who knows, you might discover the next blockbuster drug!

Want more from Nandyala? Explore practical insights to bridge the gap between lab discoveries and real-world patient care here.

References

1. Prinz F, Schlange T, Asadullah K. Believe it or not: how much can we rely on published data on potential drug targets? Nat Rev Drug Discov. 2011;10(9):712. doi:10.1038/nrd3439-c1
2. Begley CG, Ellis LM. Raise standards for preclinical cancer research. Nature. 2012;483(7391):531–533. doi:10.1038/483531a
3. Begley CG, Ioannidis JPA. Reproducibility in science: improving the standard for basic and preclinical research. Circ Res. 2015;116(1):116–126. doi:10.1161/CIRCRESAHA.114.303819
4. Morris ZS, Wooding S, Grant J. The answer is 17 years; what is the question: understanding time lags in translational research. J R Soc Med. 2011;104(12):510–520. doi:10.1258/jrsm.2011.110180
5. Seyhan AA. Lost in translation: the valley of death across preclinical and clinical divide — identification of problems and overcoming obstacles. Transl Med Commun. 2019;4:18. doi:10.1186/s41231-019-0050-7
6. Pound P, Ritskes-Hoitinga M. Is it possible to overcome issues of external validity in preclinical animal research? Why most animal models are bound to fail. J Transl Med. 2018;16(1):304. doi:10.1186/s12967-018-1678-1

Sushma Nandyala

Sushma Nandyala is a PhD Scholar in Ophthalmology at AIIMS New Delhi, specializing in infectious keratitis and corneal therapies. A gold medalist in Optometry, she has authored 15+ publications, presented internationally, and serves as a peer reviewer and Associate Editor with expertise in clinical research and scientific writing.

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