Drug Discovery Is Not Just Great Science, It Is a Roadmap

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This article is part of a short Drug Discovery Roadmap series exploring what it really takes to move from promising science to a medicine that can survive development. It includes insights from industry veterans, investors, academic and biotech who participated int the Drug Discovery Forum (Biobeacon) at ARCS 2025.

This article explores four development questions that can shape the path from promising science to medicine:

A. How do you define the product you are actually trying to build?
B. What evidence shows the drug reaches and engages the right target?
C. How do IP, manufacturing and quality decisions affect the path?
D. When does a shortcut save money, and when does it create a more expensive delay later?

It part of series.

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Biotech series:

Featuring insights from Dr Wolfgang Jarolimek, Head of Drug Discovery at Syntara; Dr Pegah Varamini, Head of the Breast Cancer Targeting and Drug Development Laboratory at the University of Sydney; and Dr Mike Lamprecht, Investment Manager at Tenmile.

Written by Angelique Greco, who brings 15+ years of experience across drug development, from preclinical research to clinical development, with a focus on translating from pre-clinical to clinical development, clinical strategy and operations.

Most researchers know the science. That is the bit we were trained for.

We know the biology, the mechanism, the assays, the early signal that makes everyone in the lab excited. There is a target. There is a way to modulate it. There is a hypothesis that, if it survives enough reality checks, may one day help patients.

But a promising discovery is not a medicine-in-waiting.

It is the start of a development path.

Between the bench and an approved medicine sits a much less romantic set of questions. Toxicity. Pharmacokinetics. Target engagement. Formulation. IP. Manufacturing. Regulation. Funding. Clinical adoption. Reimbursement. A market that may or may not behave the way the slide deck promised it would.

The overwhelm is real, and it can make the drug design look like the easy bit in the process, which is frankly rude, because that was hard enough.

I have spent the last 15 years working across drug development, preclinical and clinical development, and one thing is very clear: early programs rarely fail because the science wasn’t promising enough. They often fail because the science was not connected early enough to the development path it needed to translate and survive.

Fundamental research and drug development are not the same thing.

But any drug development program starts with fundamental academic science. Sometimes, the biotechs draws on the biology from academics and start from scratch. Sometimes the academic takes the biology one step further and start developing their own assets to modulate the biology.

Academics should not be pressured into turning every fundamental research into a drug discovery program. But if they are up for it, they should be supported.

Fundamental research and drug development programs have different objectives, different incentives and require a different skill set. So how do we bridge the two so that academic can take their science forward beyond publication and beyond the university walls?

Tech transfer office and commercialization course are important. But ultimately connecting with industry veterans and funders like Venture Capital early can help shape a sounder development program.

That’s the value of events like the ARCS Drug Discovery Forum. It is a platform to bridge this gap beyond a commercialisation course. They help researchers see the gaps that apply to their specific project, not just the theory behind it. At the forum, researchers pitch their projects to people who have seen the commercialisation path before, industry veterans, investors and drug development leaders. The event did not reveal a secret formula, because there is no bulletproof plan.

But it did make the roadmap visible.

It also highlighted the critical milestones that signal confidence, or lack of confidence, in a project's potential to become a medicine.

And for researchers, founders and early biotech teams, that roadmap matters.

Not because commercialisation is the only reason to do science.

Because research papers do not cure patients. Approved medicines do.

The gap between discovery and development is real

Tim Boyle, CEO of ARCS Australia, named one of the core issues clearly. The gap is not just funding. It is capability. There is a skills gap between founding something and taking a healthcare product all the way through the messy, expensive, highly regulated path to market.

"Innovation is driven by people. It isn't driven by startups and companies. So with people driving innovation and being a professional association, we recognise that there's a skills uplift between founding a company and being successful in commercialising and exiting the commercialisation of a particular technology and taking it to market."

That line matters because it puts language around something many researchers feel but may not have been taught to solve.

You can be excellent at discovery and still be underprepared for translation.

That is not a personal failure. It is a system issue. Universities train people to investigate, publish and expand the limits of what is known. Drug development asks a different question: can this discovery become something safe, manufacturable, protectable, fundable, testable and useful enough for the real world?

Those are not small add-ons at the end.

They shape what should be done from the beginning.

Tim put it plainly:

"You don't learn commercialisation in the classroom in a training program. There is a rough roadmap that you can take. But every technology has its own unique circumstances or peculiarities that make it not a standard playbook. I think it's more the practicalities of engaging with those that have done it before, creating an environment where people can ask the questions and not feel that they're asking silly questions."

That is the sweet spot.

There is no single playbook, but there is a roadmap. And once you understand the roadmap, you start asking different questions.

Not just, "Can we show an effect?"

But, "Can this effect become a product?"

Start with the product you are trying to become

One of the most important fundamentals in drug development is the target product profile, or TPP.

A TPP is not paperwork for people who enjoy acronyms a little too much. It is the shape of the medicine you are trying to build.

Who is it for?
What problem does it solve?
How good does it need to be?
What safety profile would be acceptable?
How will it be given?
What will it need to beat?
What would make a clinician use it?
What would make a payer, partner or investor take it seriously?

Without that clarity, "fail fast" becomes a catch phrase. To fail fast, you first need to know what failure looks like.

"To know what is a fail and what is a path you need a little clarity, and this should come in the format of the target product profile, or TPP. Define your target product profile early, very early."

I remember sitting down on my first week in academia where I had taken a research role developing a new antiparasitic molecule and asking my supervisor “okay, so what the TPP of this product, how far are we in defining it”… I had spent 2 years in big pharma, he was ex GSK but we were in academia and he was like “woo… slow down, this is an academic program, it has not gone that far yet”.

That’s where I discovered the different dynamic between working in pharma or biotech and academic program. All very smart and capable people. Different mindset, different focus, different resources, different gears.

This is where many early programs lose time.

The academic instinct is to keep generating more evidence. More assays. More mechanism. More beautifully controlled work. That work may be scientifically valid, but in development, every experiment should connect to a decision.

Dr. Mike Lamprecht, investment manager at Tenmile, was straightforward about this:

"You don't want to be spending a lot of time and a lot of money on something that's never realistically going to get to market."

That does not mean killing ideas for fun. Nobody needs a professional dream-crusher on their back.

It means asking the hard question early enough to still have options.

What experiment could kill the project?
What result would make you stop?
What result would make you pivot?
What would make an investor, clinician or pharma partner say, "Not yet"?

Those questions are uncomfortable. They are also where the discipline starts. They can save you from falling into the sunk cost fallacy, where you keep investing more time and capital to justify the time and capital already spent.

Alas.

Every experiment should de-risk the next decision

Early data is not just about proving promise. It should reduce uncertainty.

If you have a new modality, a new mechanism or a first-in-class idea, the risk is not only whether the biology looks exciting in vitro. It is whether the program has a realistic path to a safe, effective product.

Mike gave a practical example:

"Let's say you have a new antibiotic or a new therapeutic, and it's got a new modality. The first thing I would be thinking if someone's pitching me that is, have you put it into animals yet? Have you done any toxicity studies? If you haven't, that would be the fail fast suggestion right there, get it into the animals and see if they survive."

This is where "fail fast" becomes less trendy and more useful.

It is not about being reckless. It is about sequencing the right experiments so you are not spending years optimising something that has a fundamental problem.

And the point is not only toxicity.

Are you using the right comparator?
Have you benchmarked against the gold standard?
Have you tested the dose range that matters?
Do you know where the compound goes?
Do you know whether it engages the target?
Do you know whether the effect is on-target, or some secondary pharmacological effect?

Every next experiment should answer a critical question.

Target engagement is not optional

This is one of the concepts I wish more early programs took seriously from the start.

Binding data is not enough. In vitro efficacy is not enough. Tissue distribution is not enough.

You need to know whether your drug reaches the right place, at the right concentration, and engages the intended target in a living system.

Dr Wolfgang Jarolimek, Head of Drug Discovery at Syntara, explained the issue clearly:

"Pharmacokinetic studies need to be at the first stage. The second one is showing evidence that they have engaged the target, so they have blocked the mechanism that they're really interested in. If you don't show that, you may discuss auxiliary pharmacology, off-target effects rather than on-target effects."

This is one of those points that can sound technical until you realise how much time and money sits behind it.

Pharmacokinetics tells you what the body does to the drug. How much is there? How long does it stay? Where does it go? Is the exposure high enough to plausibly affect the target?

Target engagement tells you whether the drug is doing what you think it is doing.

In many cases, scientists use surrogates instead of evidence. It sounds like this: "We administered the drug, and we see a cascade of effects on the important biomarkers."

Taaadaa.

What often sits behind this is: "These effects can only be due to our drug acting on our desired target. What else could it be, right?"

Well, plenty of other things.

If you skip that link, translation becomes much weaker. You may see an effect in animals, but you do not know whether the effect is due to the mechanism you plan to take into humans.

Wolfgang went further:

"If you are inhibiting this target or activating this target in an animal, this concentration, these doses need to actually be real. You need to show that you are interfering with the target at the expected dose from your in vitro studies. If you don't have that, it's very difficult to translate into clinical studies, and that is a major deal breaker for academics going forward with biotechs or pharma."

"Major deal breaker" is the phrase to keep.

This is not a nice-to-have experiment. It is the kind of evidence that tells a serious partner whether the program has a credible bridge from preclinical promise to clinical testing.

Wolfgang also shared a cautionary example:

"A well-documented example is Simtuzumab, the LOXL2 monoclonal antibody. Gilead bought Arresto, they put it in many clinical trials and it failed in every single clinical trial. They must have spent in excess of $500 million on it. The reason was they had not actually shown target engagement."

That is not a small oops. It was later found to bind to the target without inhibiting the catalytic activity of the enzyme, failing to stop collagen cross-linking or reduce the tissue stiffness responsible for fibrosis.

That is a very expensive reminder that binding to a target and changing the target's activity are not the same thing.

If it is a targeted technology, prove it is targeted

Dr Pegah Varamini, who leads the Breast Cancer Targeting and Drug Development Laboratory at the University of Sydney School of Pharmacy, brought this principle to life.

Her work focuses on novel therapies for triple negative breast cancer, an aggressive subtype where more targeted treatment options are badly needed.

When she pitched, the panel asked about tumour uptake.

"I was asked questions about how much tumour uptake I get because this is a targeted therapy. You have to show that you get a high level of accumulation in the tumour, and that is how your technology is targeted. If you don't have data for it, then investors would come back to you and say, you have to do it before we think about it. Fortunately,I did it early on and I did have a response for it."

That is the difference between having a concept and having a development argument.

If your technology is targeted, you need to show the targeting. If your claim is tissue-specific, tumour-specific, receptor-specific or mechanism-specific, the data has to match the claim.

The molecule is not your only risk

Once the science looks strong, it is tempting to think the project is safe.

Oh how we wish!

It is not.

A program can still fail because the IP is weak, the patent clock is running, the material cannot be manufactured, the formulation is unstable, the synthesis cannot scale, the regulatory plan is wrong, or the capital was spent on the wrong next step. And then there is no more runway.

This is why drug discovery is not a single-lane road. IP, manufacturing and regulatory thinking need to run in parallel with the science. Even QC needs to be considered early, no matter how boring it may feel to the scientists designing drugs. No offence to the QC people. We need you. Badly. Please stay.

IP coverage

Beyond the fundamental questions of “Do you have freedom to operate and have you patented your IP” came an even more strategic one about IP timing.

Patenting starts the clock. And the clock runs fast.

Pegah described one of the questions she received around IP timing:

"One question was regarding the IP strategy and life of my patent. One of the panelists asked me about my thoughts around when to go for investment, and the reason was that if I go late for investment, then there is a risk of not having enough life of my patent."

That question connects legal timing to commercial value.

In academia, filing can feel like a milestone. In development, it starts a clock. File too early, and you may lose years of patent life before the asset is close to market. File too late, and someone else may block you or weaken your position.

IP is not only timing. It is also freedom to operate, claim strategy, patent families, indication coverage and whether parts of your construct, molecule or method are already owned by someone else.

The science may be yours. The path around it may not be.

That is even more true when you combine pieces that are already covered by IP. This came up in relation to clever AAV designs, but the point is broader: you need freedom to operate at multiple levels, not just on the final product. Your IP strategy needs to match that reality.

Fortunately, a good IP specialist can help not only with writing a patent, but with the whole sequencing of IPs you can use to extend patent life.

Manufacturing

Manufacturing brings another kind of reality check.

Wolfgang described how investors look at scale very early:

"The investors are very sharp and on point about the problems that are occurring in the drug discovery process, and they look at it very early on. An example is that they ask about the scale up part. If there is only very few milligrams of this compound available then how can we scale it? How can you make it?"

This is where a lab success meets the grown-up version of chemistry.

Fifteen milligrams may feel heroic when the synthesis took two weeks, twelve emotional spirals and a catalyst that costs more than your wedding ring. But it will not get you through toxicology or first-in-human planning.

Can you make grams?
Can you make kilograms?
Can someone else reproduce the process with the same purity/impurity profile?
Can the route be transferred to a manufacturer?
Can the material be made at the right grade for the next stage?

Even the grade of material can change the capital plan.

Pegah explained how this became a live strategic question for her:

"One recurring question which has sparked debate was what grade of materials to start a first-in-human study. I'm getting mixed advice. Some people say you need GMP manufactured products. Some other people say, in Phase 1 in Australia you don't need that, so why should you spend a lot of money and resources and go for GMP while it's not necessary?"

That is not theoretical.

"Non-GMP you can get away with, with like half a million for a technology like mine, and when it goes to GMP, I don't really know, but it can be up to 2 million or above."

That kind of advice can change the path of a program.

Not because one answer applies to every product. It does not. But because asking the right person, at the right time, can prevent a team from spending capital in a way that does not move the program closer to the next value inflection point. But beware. It’s not that simple.

The shortcut is not always cheaper

There were a great debate about which material should you take to a FIH. The debate was for Australia but it applies for the FDA too.

This is where cost control can get dangerous.

Every early biotech is trying to stretch capital. That is normal. No one has infinite runway, and if they say they do, check the term sheet twice.

But there is a difference between making a smart staged decision and taking a shortcut that buys you trouble later.

You see this with toxicology and manufacturing quality. A team may decide to reduce the scope of toxicology studies, use non-GLP work where GLP-standard toxicology would normally be expected, or make clinical material at a lower quality threshold because it saves money before first-in-human studies.

Firstly, and importantly, major regulators still expect quality, control and traceability. The debate should not be whether quality matters. It should sit around the level of certification, licence and documentation required for that stage.

For an FDA IND, the nonclinical safety package needs to be robust enough to support the proposed clinical trial. In practice, pivotal toxicology studies are usually run to GLP standards. The ICH M3(R2) guideline also exists to align the nonclinical safety studies expected to support human clinical trials and marketing authorisation across major regions.

The same logic applies to manufacturing quality.

For Phase 1 investigational drugs, FDA guidance recognises that these products are exempt from the full commercial GMP requirements under 21 CFR Part 211. But that does not mean “anything goes”. The product still needs phase-appropriate quality controls focused on subject safety, identity, purity and contamination prevention.

Australia follows a similar practical logic. Some medicines prepared for initial experimental studies in human volunteers can sit outside the full GMP licensing or release-for-supply requirements that apply later. But again, this is not permission to be casual. The material still needs to be suitable for human use, with appropriate quality, documentation, traceability and release controls.

The difference in cost can still be substantial and meaningful if you pursue fully licensed GMP material when it is not necessary for that stage.

So the perceived shortcut is mainly a misconception. The quality still matters. The real premium often sits at the certification or licence level.

So before celebrating the preclinical saving, ask the more expensive question.

Where is my product manufactured, what is the track record of the manufacturer, is it auditable and traceable? Will it cause delay at later stage and if so Is the saving now worth the cost of a clinical delay later?

Because once you are in clinical development, every delay gets heavier.

Cost control matters. But so does building a package that can travel.

Sometimes there is a legitimate staged path. But the question is not only, "Can we get into this first clinical trial?"

The better question is, "Will this data still be useful when we need to speak to FDA, EMA or a serious pharma partner?"

The roadmap does not make the science smaller

There is sometimes a fear that thinking commercially too early somehow contaminates the purity of the science.

Joining the dark side anyone? But there are no Jedi and Sith Lords here. You are not going to the dark side when you start thinking with a commercial mindset.

Good development thinking does not make the science smaller. It makes the questions sharper.

It asks whether the biology can survive contact with toxicity, dosing, manufacturing, clinicians, patients, partners and payers.

That is not selling out. That is taking the possibility of patient impact seriously.

If you are working on a discovery that could become a therapy, the roadmap is not an administrative burden. It is the difference between interesting work and work that has a shot at reaching the people it was meant to help.

🔎 Actionable insight: map the next killing question

Take your current project and write down the three questions that could kill it.

For each one, write:

  1. What data would reduce this risk?
  2. Who has seen this problem before?
  3. What result would make us stop, pivot or change the development path?

Then choose one person to speak to before your next major experiment, grant application or investor conversation.

Final reflection: the science is only the beginning

A promising discovery deserves more than enthusiasm.

It deserves a path.

That path will not be perfect. It will change. It will get annoying, because biology is rude and budgets are worse.

But if you can see the rough roadmap earlier, you can ask better questions, design stronger experiments and avoid confusing movement with progress.

This was Part 1 of this series looking at the scientific and adjacent fundamentals: TPP, toxicity, pharmacokinetics, target engagement, IP, manufacturing and the false economy of weak preclinical shortcuts.

Part 2 looks at the people who can change the route before the expensive mistakes do: industry veterans, investors, clinicians and pharma-minded advisors.

Because the right question, asked early enough, can save years.

And sometimes, it can save the medicine.

Continue the series:

Part 2: Why Industry Veterans Can Change the Path of a Drug Discovery Program, coming next.

2026 articles: Two more pieces will follow from the ARCS Drug Discovery Forum 2026.

Success story: Read how Dr Chris Burns helped develop Momelotinib, from lab bench to FDA approval.


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