Drug Discovery Bottlenecks Require Understanding Disease Biology Over AI Magic Wands

Drug Discovery Bottlenecks Require Understanding Disease Biology Over AI Magic Wands Daphne Koller argues that AI cannot cure diseases through computation alone because the primary bottleneck in drug discovery is our limited understanding of human biology and disease mechanisms, rather than the speed of molecular design or trial execution. More than 90% of drug candidates entering clinical trials fail, predominantly because they target the wrong biological mechanism rather than because of flaws in molecular design. Industry focus has shifted toward redundant targets, with the number of novel targets advanced annually dropping from roughly 100 in 2015 to about 30 in 2024. Large language models cannot simply reason through existing literature to find cures because human biology is messy, evolved, and lacks sufficient causal and human-specific perturbational data. Autonomous agentic labs thrive on fast, cheap feedback loops like those in coding, but drug efficacy relies on slow, expensive human clinical trials that compute cannot shorten directly. The Mechanism Bottleneck in Drug Discovery Drug discovery comprises three stages: disease-to-mechanism, mechanism-to-drug, and drug-to-patient. While tools like AlphaFold have greatly accelerated molecular design in the second stage, validated targets remain rare. Because over 90% of clinical-stage drugs fail due to pursuing incorrect mechanisms, generating molecules faster merely manufactures keys for the wrong locks, prompting companies to crowd around the same few validated targets. Data Limits in Modeling Human Biology The belief that language models can uncover mechanisms by analyzing published papers assumes all necessary biological information has already been gathered. Biological systems span multiple dynamic layers that cannot be understood in the abstract without new measurements. Existing cell atlases and virtual cell initiatives sample only a fraction of perturbations, while severe human-specific conditions like Alzheimer's disease and ALS cannot be recapitulated in animal models. Feedback Loop Challenges in Autonomous Labs Closed-loop AI agents interacting with automated lab hardware excel only when guided by fast, accurate, and cheap evaluation scorecards. While this dynamic functions well for constrained tasks such as protein synthesis or software development, the ultimate test of therapeutic efficacy is a human clinical trial. Because clinical trials take years and are bound by human biology and ethics, agents optimizing high-throughput proxy assays risk accelerating the pursuit of unviable targets. Mechanistic Insights to Improve Clinical Trials Applying AI to the clinical development phase can streamline operations like regulatory drafting and patient identification, but in-life biological observation accounts for half of the trial timeline and cannot be bypassed. The primary way AI can structurally improve trial efficiency is through mechanistic understanding that reveals early biological signals, confirms target engagement, and identifies patient subpopulations most likely to benefit.

AI制药没有“魔杖”：攻克新药研发的核心瓶颈在于理解生物学机制 针对科技界认为通用人工智能（AGI）能够迅速攻克疾病的乐观论调，insitro创始人兼CEO达芙妮·科勒（Daphne Koller）撰文指出，药物研发的核心阻碍并非分子设计效率，而是对人类疾病底层生物学机制的匮乏理解。现有AI工具多为局部优化方案，若脱离针对临床收益的有效因果模型，仅会加速产出错误靶点的失败产品。 药物研发可分为“疾病到机制”、“机制到药物”以及“药物到患者”三阶段，当前多数AI技术主要聚集于第二阶段的分子设计。 临床试验失败率超90%且数十年未见实质改善，主要原因并非分子工程缺陷，而是靶向的生物学机制错误，目前行业年均推进的新靶点数量已从2015年的约100个降至2024年的约30个。 现有生物数据高度缺乏因果与扰动测量，且阿尔茨海默病等人类特异性疾病无法在动物模型中有效复现，抽象推理无法替代实际生物学测量。 AI智能体在实验室自动化的成功依赖廉价且快速的反馈闭环，而药物的终极检验标准——人体临床试验——耗时长、成本高且无法被纯算力绕过。 优化临床试验运营仅能压缩部分前期行政与招募时间，根本性的突破仍依赖于基于生物机制识别新型生物标志物与临床读数。 制药核心痛点：缺乏正确的生物学靶点机制 大多数AI制药项目集中于“机制到药物”阶段，利用AlphaFold等工具快速设计新型分子。然而，历史上针对不可成药靶点（如KRAS）的突破主要依赖数十年的结构生物学积累或新型疗法模态拓展，而非单纯的AI分子设计。绝大多数缺乏疗法的疾病根本未知其对应机制。制药界过度拥挤在少数已知靶点上（38个靶点各自对应超50个项目），导致临床前新靶点探索急剧缩减。当前行业擅长制造“钥匙”，但大多数钥匙匹配的都是“错误的锁”。 生物数据的复杂性与人类特异性限制抽象推理 寄希望于大语言模型仅凭已有文献进行逻辑推理以发现机制是不切实际的。生物学是数十亿年随机进化的产物，涉及DNA、蛋白质、细胞及系统环境的多尺度动态响应。尽管已有覆盖数亿细胞的图谱及“虚拟细胞”项目，但在扰动和因果测量方面仍极度匮乏。更严峻的是，阿尔茨海默病、渐冻症等重疾具有高度人类特异性，啮齿类和非人灵长类模型无法有效复刻，使得关键数据获取难度极大且成本高昂。 自动化与智能体面临漫长的临床反馈闭环 智能体与自动化实验室系统在无细胞蛋白合成等受限搜索任务中表现优异，因为这些领域具有廉价、快速且精确的打分机制。然而，药物研发的终极检验标准是患者临床疗效，无法被计算模型或高通量筛查完全替代。临床验证周期长达数年且成本巨大，无法仅通过增加算力或优化流程缩短。若缺乏与人类临床获益强相关的代理目标函数，AI驱动的闭环优化只会更快地制造出错误靶点的分子。 突破临床瓶颈仍需根植于深入的机制理解 AI在预测毒理学、文书起草、电子健康档案筛选受试者等运营层面的优化，仅能压缩部分开发周期，而疾病在活体中的进展时间由生理规律决定，属于无法压缩的固有周期。真正打破临床僵局的路径在于机制洞察：通过深度理解生物机制，发掘早期生物标志物，进而筛选最适患者群体并提前验证靶向效果。唯有将核心精力投向解析致病机制，才能实现从单纯的过程优化到真正改变患者生存结局的跨越。

[America](https://www.a16z.news/t/america) | [Tech](https://www.a16z.news/t/technology) | [Opinion](https://www.a16z.news/t/opinion) | [Culture](https://www.a16z.news/t/culture) | [Charts](https://www.a16z.news/t/charts) *Today, we’re excited to share a guest post from Daphne Koller, Founder and CEO of insitro. For more from her, subscribe to insitro’s Substack [here](https://deepphenotype.substack.com/).* The tech world has latched onto an intoxicating promise: build a superintelligence, and it will cure cancer, and every other disease as well. The logic is seductive. The human body is a system we can already read from and write to, so like other knowledge problems, a powerful enough AI *should* be able to solve disease. I fully believe that AI will eventually transform human health. It is why I’ve spent close to 30 years working at the intersection of AI and biology, and the last decade in drug discovery. The need is staggering: by most counts only a quarter of diseases — and by some estimates a few percent — have an approved therapy, and most of those merely slow a disease rather than stop it. For the majority of human illness, medicine still has little to offer. But the magic-wand promise rests on an assumption that turns out to be false: that we already understand human biology well enough for a clever enough reasoner to find the cures hidden in what we know. We don’t. Hundreds of years into modern medicine, our understanding of most human disease, and much of healthy physiology, is best captured by the parable of the blind men and the elephant; in this case, a really huge elephant. AI is undoubtedly extraordinary, but aimed at a biology we have only begun to measure and barely understand, it will mostly help us generate failures faster. This essay is about what that actually takes. The path to real cures starts at the root of the problem: measuring biology in the right way and using AI to derive novel insights from those measurements. Below, I describe some of the most prevalent AI Magic Wand narratives, explain the key pitfalls, and offer my perspective on what we actually need to deliver on this important goal. To understand where AI fits, it helps to decompose drug discovery into its three essential stages: **Disease-to-mechanism:** Identifying a biological mechanism — a pathway, a target, a molecular interaction — where therapeutic intervention will alter the course of disease in humans. **Mechanism-to-drug:** Creating a molecular intervention in the right therapeutic modality — a small molecule, antibody, siRNA, gene therapy — that achieves the desired mechanistic effect with acceptable safety and pharmacological properties. **Drug-to-patient:** Designing a clinical development program that identifies the right patients and assesses the molecule’s effects — beneficial as well as adverse. The vast majority of AI work in drug discovery has focused on stage 2. This is understandable: the origin of the AI Magic Wand exuberance is the incredible achievement of AlphaFold, a field-defining *tour de force*. From this starting point, we have seen an explosion of AI tools capable of designing novel proteins, small molecules, RNA therapies, and even gene therapies. Given a biological mechanism we want to hit, it seems that AI can now design a molecule to hit it faster and better than ever before. AI will certainly generate new and better molecules at an unprecedented rate, but will it generate drugs that unlock diseases for which there is currently no meaningful treatment? There are “undruggable targets” — high-confidence mechanisms that historically we have been unable to hit. The success against KRAS, the quintessential undruggable target, shows that this journey is possible. Notably, this success emerged from decades of structural biology and medicinal chemistry, not AI; as of now, I don’t know of a single example of an AI-derived insight that has led to “drugging the undruggable.” More broadly, the biggest step functions in our ability to drug the undruggable have historically come not from better molecular design tools, but from expanding our repertoire of therapeutic modalities: first biologics, then siRNA and antisense oligonucleotides, then gene editing. Each new modality opened a class of targets that was simply inaccessible before. But an even more critical point: validated yet undruggable targets are a tiny handful in the landscape of unmet need. For the vast majority of diseases without effective treatments, we simply have no idea what the right mechanism is. More than 90% of drugs that enter clinical trials fail — a dismal statistic that has barely improved in several decades. In the large majority of cases, the molecule was engineered just fine. The mechanism it targeted was wrong. We are doing a pretty good job at manufacturing keys, but they are generally for the wrong locks. Even if AI lets us make better keys at an accelerating pace, that won’t improve our ability to identify the right locks. **The real bottleneck in making a novel medicine is disease understanding: identifying a biological mechanism whose modification actually changes the course of disease in patients.** That, far more than molecular design, is where drug discovery succeeds or fails. This mechanistic understanding is a rare commodity. And because no one likes to fail in the clinic, we are seeing industry trends that are truly destructive. There are currently 38 targets that have over 50 programs against each of them — slightly better keys for those few locks where we have strong conviction. How many variants of GLP-1 do we really need? Even worse than this misallocation of capital is the disservice to patients: the number of novel targets the industry advances each year fell from \~100 in 2015 to about 30 in 2024. That collapse is the far bigger cost: the inability to help the hundreds of millions of people for whom medicine currently offers nothing. The disease-understanding goal requires that we bridge the chasm between high-level clinical manifestations of disease in a patient and the granular cellular mechanisms in which a drug intervenes. This has given rise to a second manifestation of the AI Magic Wand. Large language models — with their super-human reasoning capabilities — will connect the dots across the vast published literature of human biology, reasoning their way to new mechanistic hypotheses. This optimism makes a very strong assumption: that the scientific community has collected — or will soon collect — enough data about human biology to contain the answer, and that we just need better reasoning to extract it. The challenge is that human biology is incredibly complex, spanning multiple interconnected biological layers — DNA, protein, cells, multi-cellular environments, entire organisms. Individual components respond dynamically to even subtle changes in related components or in the environment. Moreover, biology wasn’t engineered; it is the result of billions of years of messy, stochastic evolution, which produced staggering variation — countless genes, cell types, states, and contexts, each behaving in its own way. There is too much of it, too idiosyncratic, to reason about in the abstract. You have to measure it. How many experiments would we need? The table below is an informed attempt at a back-of-the-envelope analysis. Even if we consider only cell biology — the layer we need to interrogate biological mechanism — the space is vast. It becomes exponentially more vast when we consider that a drug is an intervention, so we need to map not only biology as it is, but also how it would respond to a perturbation. The largest cell atlases assembled to date, now spanning hundreds of millions of cells, remain orders of magnitude too small to cover this space. Until recently they also held almost no causal, perturbational data, the measurements most critical for understanding what an intervention would do in a living system. That has begun to change: several organizations have launched the monumental effort of building a “Virtual Cell,” pairing large-scale perturbation data with AI to reduce the data collection burden. But even the largest of these efforts samples only a vanishing fraction of the possible perturbations, and does so almost entirely in a narrow range of cell lines. Even more importantly, the virtual cell efforts — useful as they might eventually turn out to be — do not address the other half of the equation: relating biological mechanisms to human clinical outcomes. Most human disease is a systems-level dysfunction, involving a complex, temporal interaction of multiple biologies spanning diverse cell types. Understanding these processes requires systems-level measurements that are far less scalable, often requiring living organisms. Which brings up the greatest data challenge. While some processes are conserved across all forms of life, others are far more specific. The folding of a single protein is a self-contained process, highly conserved — closer to physics than to biology; this allows protein folding models to be trained on sequences collected across thousands of species. Metabolism involves at least a dozen distinct cell types and might be conserved across mammals. Brain function and dysfunction involves dozens of distinct cellular identities; and these processes are exquisitely specialized to humans: rodents do not get Alzheimer’s disease; non-human primates do not recapitulate ALS. The diseases where we have made the least progress tend to be precisely those that are most human-specific, and therefore those for which the data is most expensive to collect, least available, and most fraught with ethical constraints. But we don’t need a universal causal model in order to make medicines. We can instead build a targeted causal model that makes the space navigable toward a desired outcome — uncovering the biological mechanisms underlying human diseases. Our models will not cover all biologies or all diseases, but an informed selection process will still allow us to make considerable headway. This insight motivates the thesis behind a third AI Magic Wand: swarms of AI agents operating in a closed loop with laboratory automation, relentlessly chipping away at scientific problems. They formulate hypotheses, direct robots, analyze results, and iterate. Early successes here have been beguiling — automated systems have already excelled at tasks like optimizing cell-free protein synthesis or designing antibodies against known targets. But agentic iterated optimization relies on a fundamental attribute: **agents thrive when there is a fast, accurate, and cheap scorecard to evaluate progress.** If you give a sufficiently smart model an instant feedback loop, it will grind against that benchmark until it wins. This is why coding assistants and molecular design tools advanced so rapidly — the feedback is cheap, accurate, and fast. A compiler immediately verifies whether code will run. The iterative loop with a developer provides rapid feedback on intent. The closed loop is tight, cheap, and objective. Drug development is the exact opposite. The ultimate scorecard — whether a drug actually provides therapeutic benefit to a patient — cannot be captured well by computational models or high-throughput assays. The only true ground truth is a human clinical trial. This feedback loop currently takes years, costs millions, and is strictly bound by human ethics and living biology. It is the ultimate slow feedback loop, and no amount of compute or process optimization can change this. The agentic lab successes listed above are solving problems that look like coding: highly quantitative objectives within a constrained search space. These problems are valuable, but largely beside the point when it comes to predicting whether a drug will actually work in a patient population. You cannot solve the human translation problem by accelerating our ability to optimize the wrong objective function. Doing so will simply scale up our process for building more keys to the wrong locks. In order to leverage the power of agentic AI and lab automation towards the goal of improving scientific discovery, we must first have an objective function that is a proxy to human clinical benefit, and yet allows for AI insights and rapid experimentation. Some have argued that the most important AI unlock in drug discovery is in the third stage — drug-to-patient — taking a drug candidate through preclinical testing and clinical trials. This is the fourth AI Magic Wand: reduce the time and cost of this very expensive phase, and drug discovery becomes faster and cheaper. Sadly, **if you accelerate a pipeline full of drugs aimed at the wrong mechanisms, all you get is faster failures**. At the same time, there are real opportunities for AI in clinical development: predictive toxicology models and AI-drafted regulatory filings can shorten IND-enabling work, and patient identification from electronic health records, smarter site selection, and automated data management can trim operational overhead. These compression levers offer meaningful benefits, and we should absolutely pursue those. But these gains sit almost entirely within the first two slices of work. The remaining 50% — in-life biological observation — is gated by how fast disease unfolds in a living human. Even a comprehensive AI-driven improvement across everything it can touch leaves the majority of development time and cost structurally unchanged. There is, however, one pathway through which AI could accelerate even this irreducible clock — and it runs directly through biological mechanism. An AI-enabled, deep mechanistic understanding of a disease enables the identification of novel clinical readouts that serve three distinct purposes: selecting the patients most likely to respond, confirming that the drug is hitting its intended target, and detecting early and reliable signals that it is actually modifying disease biology. Together, these allow trials to enroll the right patients, read out faster, and catch failures earlier — changes that transcend clinical trial operations, transforming the trial design itself. This capability is inseparable from solving the disease-understanding problem; they are one and the same. **Better trials, in the end, are downstream of better biology.** The AI Magic Wands described above have real value. Generating molecules quickly can be a significant accelerant, as is reasoning across the vast scientific literature and increasing the efficiency of the scientific process. But these tools are just that: point solutions that address important problems without altering the fundamentals of our industry. To fulfill the promise of AI for the millions of patients lacking any meaningful treatment, we must direct our efforts toward the problem that really matters: the identification of biological mechanisms with disease-transforming clinical benefit. This is arguably the hardest problem in drug discovery, because the only conclusive test of whether we have correctly identified a novel biological mechanism is a human clinical trial. There are multiple other paths in this space with shorter timelines and clearer near-term proof points. Those paths are shorter because the problems are more tractable: the feedback loops are faster and the benchmarks are cleaner. But a shorter path to a smaller destination is still a smaller destination — process improvements for problems we already know how to solve. For the hundreds of millions of patients for whom no meaningful medicines exist, the difference between a wrong mechanism and the right one is the difference between another devastating clinical failure and a life-altering breakthrough. That is what we need in order to truly deliver on AI’s promise for human health. *This harder but aspirational path is the one we have elected to take at insitro, and we’ll have more to say about our approach soon.* *This newsletter is provided for informational purposes only, and should not be relied upon as legal, business, investment, or tax advice. Furthermore, this content is not investment advice, nor is it intended for use by any investors or prospective investors in any a16z funds. This newsletter may link to other websites or contain other information obtained from third-party sources - a16z has not independently verified nor makes any representations about the current or enduring accuracy of such information. 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