跳到正文
AI 科研动态
元研究

为什么 AI 还没治愈癌症？Ecotone AI 沙龙探讨因果遗传学路径

Why hasn’t AI cured cancer yet?

SF AI Science StudioMichael Raspuzzi未入选
阅读原文

摘要

Ecotone AI 创始人 eMalick Njie 在沙龙预读材料中指出，AI 已能预测蛋白复合物、从头设计抗体并评分人类基因组全部单碱基变异，但临床影响仍"令人失望地有限"。2026 年一篇综述称多数 AI 原研资产仍处临床前，逾 90% 进入试验的药物仍失败；有人类遗传学支持的靶点成功率约高 2.6 倍。Ecotone 押注因果遗传学，从罕见病入手，基因组计算成本低于 1 美元。

摘要由模型根据原文撰写，以原文为准。

正文 · 原文

Humans vs. Cancer

Here’s the pre-read for our salon, “Why hasn’t AI cured cancer yet?”, with eMalick Njie, founder of Ecotone AI.

Everything in here comes from the readings you sent in as recommended pre-reading. Footnotes are at the bottom, each with a short summary of the piece and who recommended it.

It’s about a 12-minute read.

tl;dr

  • The models are real. AI now predicts protein complexes, designs antibodies from scratch and scores every possible single-letter change in the human genome.

  • The clinic hasn’t moved much. A 2026 review calls AI’s clinical impact “disappointingly limited”, and more than 90% of drugs entering trials still fail, usually because the biology was wrong.

  • We’re searching under the streetlight. The biggest saving is fewer phase II failures, but most AI effort goes to early hit-finding, where the clean data is.

  • What moves the odds is knowing the Why. Targets with human genetic support succeed about 2.6x more often, and trials that pick patients by biomarker cost about half as much per approved drug.

  • Ecotone is betting on that layer: causal genetics, starting with rare disease and genomes processed for under $1 of compute. Tonight’s question is how far it reaches into cancer.

Contents

  1. The Story of Humans and Cancer

  2. The Robots Arrive

  3. The Streetlight Problem

  4. The Scoreboard Problem

  5. The Plumbing

  6. The Cause Hunters

  7. So, What Would We Need to Know?

Part 1

The Story of Humans and Cancer

Let’s zoom way out.

For most of history, cancer happened to you, you died, and nobody was sure why. Then, about a hundred years ago, humans did what humans do best: squinted at things and sorted them into piles.

In 1925, two doctors named Bailey and Cushing looked at more than 400 brain tumors under a microscope and sorted them by how they looked.1 For the deadliest brain tumor, glioblastoma, average survival in the 1950s was about three months, partly because many doctors didn’t bother treating it. Then came roughly 70 years of surgery, chemotherapy and radiation, and survival climbed to about 14 or 15 months.

Glioblastoma under the microscope. For most of the 20th century, this view was the main way to tell brain tumors apart. Image: Wikimedia Commons, CC BY-SA 3.0.

Linear scale. Figures as reported by BrainFacts/SfN.1

Seventy years of brilliant, exhausting effort bought about a year.

Meanwhile, the economics were doing something weird. You’d expect drug-making to get cheaper over time, the way everything with a chip in it does. Instead, the number of drugs approved per billion dollars of R&D has halved about every nine years since 1950, an 80-fold decline. People call this Eroom’s Law, which is Moore’s Law spelled backwards, which is the kind of joke you make when the alternative is crying. An average oncology drug cost about $4.4 billion to develop over 2017 to 2020.2

Then, in 2001, a moment of enormous optimism. The Human Genome Project had read our whole instruction manual. Surely, people figured, with the full parts list in hand, finding new things to aim drugs at would get way easier. A 2001 prediction said the number of drug targets would grow by at least an order of magnitude, and that checking whether a target is any good would become high-throughput.3

Here’s how that went:

A sketch, deliberately not to scale. The expectation comes from a 2001 prediction cited by Bender et al.; the 2015 and 2024 counts of novel targets entering industry are from Daphne Koller.34

Instead of an explosion of new targets, the industry piled onto old ones. Koller counts 38 targets that each have more than 50 drug programs chasing them.4 Picture 50 companies picking the same lock while thousands of other doors sit unopened.

Part 2

The Robots Arrive

Fast-forward to the 2020s, when AI got good at biology. Really good.

AlphaFold 3 can predict how proteins, DNA, RNA and drug molecules fit together, and it beats the classic docking software at it.5 David Baker’s lab used RFdiffusion to design antibodies from scratch against a spot they chose in advance, and when they checked with cryo-EM, one design matched the plan to within 0.9 ångströms, less than the width of a typical atom.6 And this fall, DeepMind’s AlphaGenome Atlas scored the effect of every one of the roughly nine billion possible single-letter changes in the human genome. In a rare-disease cohort it put the real culprit variant in its top 50 for 29.5% of cases, versus 12.5% for the standard tool.7

A protein as structural biologists draw it: ubiquitin, with helices in blue and strands in green. Predicting shapes like this from sequence is the problem AlphaFold cracked. Image: Wikimedia Commons, public domain.

Linear scale. From the AlphaGenome Atlas preprint.7 A real gain, and still a ranked list of suspects, not a confirmed cause.

So naturally, the question everyone’s asking is: it’s 2026, the robots can read DNA and design antibodies, so why hasn’t AI cured cancer?

And the honest scorecard is a little awkward. A big 2026 review by Andreas Bender, Jack Scannell and colleagues describes AI’s clinical impact in drug discovery as “disappointingly limited.” Most assets at AI-first companies are still preclinical, a few dozen are in phase I or II, and very few have reached phase III.3 To be fair to everyone, the authors are careful here: they call it an absence of evidence, which is a different thing from evidence of absence. It’s early.

Here’s my pitch for tonight. “Why hasn’t AI cured cancer?” is the wrong question. It’s like buying a car that does 200 miles an hour and then asking why you haven’t arrived yet, when nobody ever gave you the address.

The better question: What would we need to know to cure a given cancer, and why don’t we know it yet?

Spoiler: the answer involves streetlights, scoreboards and plumbing more than model size.

Part 3

The Streetlight Problem

There’s an old joke. A guy is searching for his keys under a streetlight. A cop helps him look for a while, then asks, “Are you sure you dropped them here?” The guy says, “No, I dropped them in the park. But this is where the light is.”

Bender’s team uses exactly this image to describe where AI effort in drug discovery has gone.3 They built a cost model asking: if you made one stage of drug development 20% better, which stage would save the most money per drug that actually launches? The answer was clear. The biggest saving comes from cutting failures in phase II.

What is phase II?

A drug’s life in humans goes roughly phase I, II, III. Phase I asks “is this safe, and how does the body handle it?” Outside oncology, that usually means a small group of healthy volunteers. Phase II is the first time you seriously ask “does it actually work?” in a larger and messier group of real patients, at real doses. It’s where reality gets a vote.

So phase II is where a drug finds out whether the scientists were right about the biology. If they weren’t, everything spent before that point evaporates.

And where has most AI effort gone? Preclinical hit-finding, meaning the early search for molecules that stick to a target. That’s where the labeled data lives, so that’s where the light is. The keys are in the park.

Daphne Koller puts it another way.4 She splits drug discovery into three jumps: disease to mechanism, mechanism to drug, and drug to patient. AI has sped up the second and third jumps. But more than 90% of drugs that enter trials fail, and usually the molecule did exactly what it was designed to do. The mechanism was just wrong. Let’s call that first jump the Why Step: figuring out which piece of biology, if you poked it, would actually help this patient. Speeding up everything after a wrong Why Step just gets you to failure faster, in a nicer car.

So what does move outcomes? Bender’s team has a short list, and two items jump out.

First, projects that use biomarkers to pick which patients get the drug cost only a little over half as much per approved drug as projects that don’t.3 Second, targets with human genetic support are about 2.6 times more likely to succeed in the clinic.

What does “genetic support” mean?

Imagine you want to block protein X to treat a disease. “Genetic support” means there’s evidence from human DNA that X is involved: say, people born with a variant that changes X are more or less likely to get the disease. Nature already ran the experiment for you, on real humans, over a lifetime.

That’s why it’s so valuable. It’s a clue about the Why Step that comes from people, instead of from a mouse or a dish. The 2.6x figure comes from Minikel and colleagues (2024), as summarized by Bender’s team.3

Linear scales. Both from Bender et al. (Table 1 and Fig. 1b).3 Both levers are about knowing the right biology in the right patients.

Both of these are answers to the Why Step. And the flip side shows up in glioblastoma. A 2017 trial added checkpoint inhibitors to Avastin and found no survival gain, and some researchers think that’s because patients were enrolled without matching them to their tumor’s molecular profile.1 Bender’s team gives the classic positive example: imatinib works in leukemia driven by BCR-ABL and doesn’t in cases with other drivers. Same disease name, different Why.3

Glioblastoma survival today: still about 15 months.

Part 4

The Scoreboard Problem

So point the AI at the Why Step? People are trying, and the results are humbling. A quick tour:

Predicting how cells respond. Seven deep-learning “virtual cell” style models, including scGPT and Geneformer, were tested on predicting how cancer cells’ gene activity changes after genetic tweaks. None beat deliberately simple baselines, like assuming the effects of two changes just add up.8 (A follow-up paper disputes this, so the fight is live.)

Predicting which trials will work. TrialBench, built from public trial records, gets an ROC-AUC of about 0.73 for predicting phase III approval. Predicting why a trial fails scores 0.48 to 0.57.9

What does an AUC of 0.5 mean?

AUC measures how well a model ranks winners above losers. A score of 1.0 means it’s perfect. A score of 0.5 means it’s doing exactly as well as a coin flip. So a model that explains trial failures at 0.48 to 0.57 has learned roughly nothing about the Why. Bender’s team adds a sharper warning: two models with similar AUC can have opposite practical value, depending on the decision you use them for.3

Baseline multimodal model results from TrialBench.9 Safety questions score well; the Why question scores like a coin flip. Some safety scores are flattered by class imbalance.

Designing antibodies. Those gorgeous RFdiffusion antibodies? Per-target hit rates were 0 to 2%, with up to about 9,000 designs screened per target, and starting affinities needed roughly 100-fold improvement in the lab. One binder for a neuroblastoma target was beautifully specific and then didn’t kill tumor cells when built into a CAR-T.6

Binding versus working. Flory says its dynamics-aware model recovered a more-than-200-fold potency cliff in a blinded, historical Roche series that the industry-standard FEP+ predicted as about 2-fold.10 Their point: sticking to a protein and doing the right thing to it are different problems. Bender’s team makes the same point with a count: over a million known ligands, about a thousand marketed drugs.3

Notice the pattern? AI shines where there’s a fast answer key, and struggles where the answer key is a patient’s life, years later.

This is where Rich Sutton’s famous essay “The Bitter Lesson” comes in.11 Sutton’s argument: in chess, Go, speech and vision, general methods that scale with compute eventually crushed human-crafted expertise.

But every one of those wins had a Scoreboard. You win the game or you don’t. The word was transcribed right or it wasn’t.

Michael Hla’s Pro-1 shows how well this works when a scoreboard exists. It used a protein-energy simulator called Rosetta as its reward, and a critic loop pushed its success rate to 71%.12 There’s no Rosetta for “the patient is alive in five years.” In the wet lab, Benchling’s benchmark found the best model, Opus 5, solves 59% of real protocol-troubleshooting problems, because the literature records clean results and almost never the messy failures.13

Agents help with the computational half. Paper2Agent turns papers into tools an AI can run, and scored 91.2% on test questions versus 80.3% for Claude Code with Sonnet 4 alone. But 26 of 100 papers couldn’t be converted at all, mostly from missing code, data or software environments.14 And the strangest data point of all: GPN-Star, a 200-million-parameter genome model that builds evolution into its design, reached state of the art on most variant tasks after training for days on 8 GPUs. Evo 2 used more than 2,000 GPUs for months.15

Tiny aside: that’s roughly a thousandth of the compute. Sutton fans in the room, please bring your rebuttals.

Part 5

The Plumbing

If you want to see what curing one cancer actually took, read Elliot Hershberg’s essay on Sid Sijbrandij, the GitLab cofounder.2

Sid was diagnosed with osteosarcoma in late 2022. After standard treatment, it came back in 2024, and he wasn’t eligible for any trials. So he treated it like a company, with three rules. Maximal diagnostics. Ten-plus personalized treatments. Run them in parallel, not one after another.

Single-cell sequencing showed his tumor cells were making fibroblast markers, including one called FAP. That pointed to a FAP-targeted radioligand therapy available in Germany. It shrank the tumor enough to operate. After surgery and a combination of follow-up treatments, T cells went from 19% to 89% of the immune cells in the tumor. He’s now in remission.

Look at what nearly stopped it. None of it was a shortage of intelligence. Hospitals store tissue in formalin blocks that wreck the RNA you’d want to sequence. Hospital review boards behaved like a “vetocracy,” while the FDA accepted each of his five expanded-access requests within 48 hours. And the analysis was done by human computational biologists, with AI nowhere in the starring role.

Then Sid dropped the line that should haunt everyone in this room:

Areas drawn to scale. The $1M square is the speck at right: one-thousandth of the $1B square. Figures as reported in Hershberg’s essay; $1B vs $1M is Sid’s own comparison.2

About $1 billion to approve a drug. About $1 million to dose one person with a personalized therapy. That speck in the chart is the size of the opportunity sitting inside our Plumbing: the tissue storage, data access, consent and review systems that decide whether anyone can learn the Why for a given patient at all.

The tools that help today are mostly measurement tools. UCLA’s platform bioprints a patient’s tumor organoids into plates and uses AI to track how each one responds to hundreds of drugs, catching rare resistant clones; so far it’s been shown on cell lines and one patient sample.16 SPARXS, from Joo and colleagues, measured the kinetics of 4,096 DNA sequences in a single sequencing run, covering 99.9% of the library, and a physical model explained 91% of the variance in rates.17 Mostly, just more of the right measurements.

An organoid: a tiny lab-grown copy of tissue, here grown from tumor-prone mouse intestine. Platforms like UCLA’s grow these from a patient’s own tumor and watch how each one responds to drugs. Image: Abhimanu Pandey, Wikimedia Commons, CC BY 4.0.

Washington has reached the same diagnosis. The Genesis Mission has announced more than $5 billion in commitments across 15+ agencies, including a pediatric cancer challenge.18 ARPA-H’s RAPID program has four awards under way, about $83 million in total, mostly to build rare-disease data infrastructure.19 Data first, models second.

Part 6

The Cause Hunters

Ecotone’s thesis, in one sentence: causal genetic mechanisms are the missing infrastructure layer for medicine.20 In our language, Ecotone wants to industrialize the Why Step. And if you’re looking for outside evidence that this is the right place to dig, Bender’s 2.6x is it. Human genetic evidence is the one input on their list that reliably raises clinical success.

The company is starting with rare disease, about 10,000 genetic diseases where a single faulty piece of DNA can explain the whole thing. That’s the cleanest version of the Why Step.

A DNA sequencer. Reading a genome is now cheap; processing and storing what comes out is the next cost to crush. Image: Konrad Förstner, Wikimedia Commons, CC0.

Their latest paper, Embarrassingly_FASTA (February 2026), goes after the floor of the building: the cost of turning raw sequencer output into usable variants.21 Their GPU pipeline processes a 30x human genome in about 35 minutes, versus about 15 hours on CPUs, so it becomes cheap to keep the raw reads and recompute everything as tools get better.

Cost to process one 30x human genome from raw reads to variants. The vendor figure averages quotes Ecotone requested in January 2026; the other three bars are compute cost, measured in the paper.21

Cheap processing matters because of what they found when they ran it. Across just 60 diverse genomes, the count of unique variant sites passed 30 million and was still climbing, with African-ancestry genomes carrying the most variants. Most human variation is still unsampled. We’ve been searching for causes under a very particular streetlight.

The modeling side is dnaSORA, a diffusion transformer the company says can map disease-causing regions of the genome from several dozen genomes rather than the thousands that standard approaches need.20 That would change the economics of the Why Step for conditions with only a handful of patients.

Which leaves the big open question for tonight. Rare disease is inherited, and often one gene. Cancer is somatic, made of competing clones, and it changes under treatment. How far does causal genetics reach into a disease that keeps rewriting its own DNA?

Part 7

So, What Would We Need to Know?

Humans spent a century sorting cancers by how they look, then a decade building machines that read, fold and design molecules at superhuman speed. Both were real progress, and both mostly lit up parts of the problem that already had light.

Here’s the reframe I’d offer. AI hasn’t cured cancer because curing cancer is mostly a Why problem, and we’ve been giving our smartest machines What problems. What does this protein look like? What sticks to it? What does this variant probably do? Those questions have answer keys. The Why questions (which mechanism, in which patient, and how would we know?) don’t have answer keys yet. Someone has to build them.

The bottleneck for AI in cancer is the Scoreboard. Whoever builds a fast, honest scoreboard for the Why Step gets to run the Bitter Lesson on biology.

That scoreboard could be causal genetics, dense measurement like SPARXS, patient organoids, or N-of-1 data from people like Sid. Probably all of these. Which raises a better question than the one on the invitation: once that scoreboard exists, what happens to the Eroom curve?

Nobody knows yet. Come argue about it.

Discussion Guide

Four threads for the room.

1. Biological data collection and structure

  1. Where is the biggest bottleneck right now: generating new data, standardizing what exists, or getting access to data locked inside pharma, hospitals, and academic labs?

  2. Which kinds of data matter most for AI that we’re barely collecting today (longitudinal, single-cell, perturbation, negative results)?

  3. What would it take for a lab, CRO, or self-driving lab to produce AI-ready data by default instead of cleaning it up afterward?

  4. Who should fund and own shared datasets, and what incentives would get competitors to contribute?

2. Limits of current ML models

  1. Where have reasoning LLMs with tools and custom harnesses actually surprised you in science, and where do they consistently fail?

  2. Can AI discover biological mechanisms that have never been observed, measured, or described in the scientific literature?

  3. Are today’s architectures fundamentally limited by what they were trained on? When do we need entirely new approaches, such as diffusion models, rather than better reasoning, harnesses, or more compute?

  4. How should we evaluate scientific AI when the real test is wet-lab or clinical validation that takes months or years? Is it possible to no-longer need wet-labs?

3. Clinical infrastructure gaps

  1. If AI made drug discovery 10x faster tomorrow, where would the pipeline jam next: preclinical validation, manufacturing, trial recruitment, or regulatory review?

  2. Why is patient recruitment still so slow, and what would change it (decentralized trials, EHR matching, patient registries)?

  3. What could adaptive trial designs, synthetic control arms, or digital twins realistically replace, and what will they never replace?

  4. Who is building the “picks and shovels” of clinical infrastructure, and why hasn’t more capital flowed there?

4. AI regulation and the frontier

  1. It makes sense to regulate AI agents that engage in harmful or criminal behavior. But should the same restrictions apply to AI systems working to cure cancer and genetic diseases?

  2. Should AI regulation focus on what a system actually does and the risks it creates, rather than the underlying model or its computational capabilities?

  3. What are the human costs of slowing scientific AI, measured in delayed diagnoses, treatments, and potentially preventable deaths?

  4. How do we prevent dangerous misuse without restricting the frontier capabilities that could accelerate lifesaving scientific discoveries?

Acknowledgements

Thank you to our dinner partner.

  • Ecotone AI is building genetic mechanisms to solve the Grand Challenge of curing 10,000 rare diseases.

Thanks to our community partners for helping make this happen.

  • Fifty Years is a pre-seed and seed focused VC firm that backs founders using technology to solve the world’s biggest problems.

  • Columbia Venture Community, Bay Area Chapter brings together Columbia University alumni founders, investors and innovators to exchange ideas, share expertise and create opportunities across the Bay Area startup ecosystem.

  • Worldwide Studios is an education non-profit that hosts summits, hacks and workshops to help engineers, scientists and professionals build with the latest in AI, hardware and applied sciences.

Footnotes

  1. Karen Hopkin, “A History of the Classification of Glioma Brain Tumors”, BrainFacts/SfN, Oct 2019. Recommended by Yuni.

    How doctors have sorted brain tumors, from Bailey and Cushing’s 1925 study of 400+ tumors under the microscope to molecular profiling (TCGA, MGMT, BRAF). The takeaway: one-size-fits-all treatment is giving way to tumor-specific strategies, while glioblastoma survival is still about 15 months.

  2. Elliot Hershberg, “Going Founder Mode On Cancer”, The Century of Biology, Jan 18 2026 (Eroom’s law per Scannell et al. 2012; $4.4B oncology figure from a 2017–2020 analysis, both as cited in the essay). Recommended by Greg.

    GitLab cofounder Sid Sijbrandij’s “founder mode” fight against recurrent osteosarcoma: maximal diagnostics, 10+ personalized therapies run in parallel, and a FAP radioligand that made his tumor operable. The hardest obstacles were tissue access, sequencing and hospital review boards, and humans, not AI, did the analysis.

  3. Bender, Thomas, Scannell, Shaywitz et al., “Artificial intelligence in drug discovery: what it is, where we stand and the path forward”, Nat Rev Drug Discov, Aug 2026. Phase II cost model (Fig. 1), biomarker stratification (Fig. 1b), 2.6x genetic support (Table 1, from Minikel et al. 2024), 2001 target prediction, imatinib, AUC example (Fig. 5), ligand counts (Box 1). Recommended by Natalie.

    Sixteen authors assess where AI in drug discovery really stands and find little clinical impact so far. The biggest lever is fewer phase II failures and better patient selection, yet most AI effort goes to early hit-finding. They call for human-relevant data, causal genetics and benchmarks that measure better decisions.

  4. Daphne Koller, “Drug Discovery Has No Magic Wands”, a16z, Aug 3 2026. Recommended by Robert.

    insitro’s CEO argues there is no magic wand: the bottleneck is finding the disease mechanism that matters in humans, not designing molecules or running trials faster. More than 90% of trials fail, mostly on wrong mechanisms, so we need to measure human biology at scale and build targeted causal models.

  5. Abramson et al., “Accurate structure prediction of biomolecular interactions with AlphaFold 3”, Nature, May 2024. Recommended by Mariia.

    DeepMind and Isomorphic’s model predicts the joint 3D structure of proteins, DNA, RNA, small molecules and modified residues, beating specialist docking tools. Limits include static snapshots, invented structure in disordered regions and heavy sampling for hard targets like antibodies.

  6. Bennett, Watson … Baker, “Atomically accurate de novo design of antibodies with RFdiffusion”, Nature, Nov 2025. Recommended by Karthik.

    The Baker lab designs antibodies from scratch against chosen epitopes, and cryo-EM confirms the designed poses at near-atomic accuracy. Hit rates were 0 to 2% per target, and binders needed lab maturation to reach therapeutic-grade affinity.

  7. Ewen Callaway, “DeepMind’s new genome ‘atlas’ charts effects of all nine billion human gene mutations”, Nature, Sep 9 2026, recommended by Daniel; primary paper: Cheng et al., “AlphaGenome Atlas”, preprint, 2026.

    Nature’s news story and DeepMind’s preprint on a precomputed map of predicted effects for all ~9 billion possible single-letter changes in the human genome. It ranks non-coding variants better than prior tools and helped solve a rare-disease case; it is research-use only and has no tumor benchmark.

  8. Ahlmann-Eltze, Huber & Anders, “Deep-learning-based gene perturbation effect prediction does not yet outperform simple linear baselines”, Nature Methods, Aug 2025. Recommended by Clayton.

    A head-to-head test of seven deep-learning and foundation models at predicting gene-expression changes after genetic perturbations. None beat deliberately simple additive or linear baselines, a call for tougher benchmarking of “virtual cell” claims.

  9. Chen, Hu … Fu, “TrialBench: Multi-Modal AI-Ready Datasets for Clinical Trial Prediction”, Scientific Data, Sep 2025. Recommended by Sebastian.

    23 AI-ready datasets across 8 clinical-trial prediction tasks, built from ClinicalTrials.gov and DrugBank. Baseline models predict safety outcomes well, phase III approval only moderately (AUC 0.73) and the reasons trials fail at roughly chance.

  10. Winnie Luo, “Can we design drugs backwards?”, Flory Notes, Oct 7 2026 (company-reported, retrospective test). Recommended by Winnie.

    Argues drugs should be designed backward from the protein state you want, because binding is not the same as function. Flory reports a dynamics-aware model that caught a >200x potency cliff FEP+ missed, with cancer examples like RAF-MEK and mutant p53.

  11. Rich Sutton, “The Bitter Lesson”, Mar 13 2019. Recommended by Amit.

    Seventy years of AI history show that general methods which scale with compute (search and learning) beat hand-built human knowledge, from chess and Go to speech and vision. The lesson: build systems that discover, not systems that contain what we already know.

  12. Michael Hla, “Pro-1”, Mar 2025 (in-silico results). Recommended by Jonathan.

    An open reasoning LLM trained with reinforcement learning against a Rosetta energy score to propose protein-stabilizing mutations. All results are computational, and the author lists the caveats candidly, including the risk of gaming the reward.

  13. Ashu Singhal, “Can LLMs work in the wet lab?”, Benchling, Aug 13 2026 (vendor benchmark). Recommended by Ian.

    Introduces BenchBench-Protocol, a benchmark built from real wet-lab protocol fixes. The best model solves 59% of tasks; models miss the tacit, messy lab knowledge that published papers leave out.

  14. Miao, Davis, Zhang, Pritchard & Zou, “Reimagining research papers as interactive and reliable AI agents” (Paper2Agent), Nature, Sep 16 2026. Recommended by Carolina.

    Stanford’s framework turns research papers into AI agents (MCP servers) that can rerun and extend the paper’s analyses. It converted 74 of 100 biology papers and beat general coding agents on test questions.

  15. Ye, Benegas … Song, “Predicting genome-wide functional constraints with GPN-Star”, Nature, Sep 9 2026. Recommended by Miyu.

    A genome language model that builds the evolutionary tree of species into its architecture. It reaches state of the art on most variant-effect tasks while using a small fraction of the compute of much larger models.

  16. UCLA Health, “New AI-powered platform helps researchers find promising cancer therapies faster”, Jun 22 2026 (Nature Protocols). Recommended by Geetika.

    UCLA’s platform 3D-bioprints patient tumor organoids into plates and uses label-free imaging plus AI to track each organoid’s response to hundreds of drugs. It has been validated so far on cell lines and one patient sample.

  17. Severins … Joo, “Single-molecule structural and kinetic studies across sequence space”, Science 385:898-904, Aug 2024. Recommended by Naveen.

    Pairs single-molecule fluorescence with DNA sequencing to measure structure and kinetics for thousands of sequences in one run, then fits a physical model to the data. A model for generating the dense, mechanistic data AI needs.

  18. White House, Genesis Mission update, Jul 22 2026; DOE, National Science & Technology Challenges. Recommended by Christian.

    The DOE-led national effort linking supercomputers, federal datasets and autonomous labs for AI-driven science. Health challenges include faster drug discovery, pediatric cancer and chronic disease, with more than $5B in commitments announced in July 2026.

  19. ARPA-H, RAPID program awards (UNC, Sage Bionetworks, FDNA, Probably Genetic), Sep 2026. Recommended by Anna.

    Four ARPA-H awards, about $83M in total, to UNC, Sage Bionetworks, FDNA and Probably Genetic to build large multimodal rare-disease datasets and AI diagnostics, aimed at shortening the ~6-year diagnostic odyssey.

  20. Ecotone AI, company site; Koreniuk & Njie, “dnaSORA: A Unified Diffusion Transformer for DNA point clouds”, bioRxiv, Jan 2025.

    Ecotone builds genetics-first foundation models to find the DNA changes behind about 10,000 rare genetic diseases. dnaSORA, a diffusion transformer trained on synthetic data, is designed to map disease regions from dozens of genomes rather than thousands.

  21. Walsh & Njie, “Embarrassingly_FASTA: Enabling Recomputable, Population-Scale Pangenomics…”, bioRxiv, Feb 2026. The $121 figure is an average vendor quote; the other costs are compute only. Recommended by eMalick.

    Ecotone’s GPU pipeline processes a 30x human genome in about 35 minutes for about $0.96 of compute, keeping raw reads so every analysis can be recomputed as tools improve. Across 60 diverse genomes, the count of new variants was still climbing.

More Resources

Other guest picks and related reading that didn’t make it into the story:

Image Credits

注意转载授权 · 阅读原文

来源：SF AI Science Studio · sfaisciencestudio.substack.com

引用原文

Michael Raspuzzi. Why hasn’t AI cured cancer yet?[EB/OL]. (2026-10-13)[访问日期]. https://sfaisciencestudio.substack.com/p/why-hasnt-ai-cured-cancer-yet.