What would you aim AI at first in science, and what discovery do you want by 2066?

What I would build first is a public AI-biology foundry: a network of automated labs that run standardized perturbation experiments on human cells, organoids, immune co-cultures, and eventually safer animal and clinical-adjacent systems. The foundry would not just collect omics data. It would generate causal data: perturb this gene, cytokine, drug, metabolite, mechanical condition, microbial product, or cell-cell interaction; measure the consequences over time; repeat across genetic backgrounds; publish the results in reusable form. AI would be used for active learning: choosing the next experiment because it is maximally informative, not because it sounds elegant.

This is possible today in pieces: lab robotics, single-cell sequencing, imaging, CRISPR perturbation, protein models, literature-mining systems, and active-learning algorithms all exist. What does not yet exist at sufficient scale is the disciplined integration, the shared standards, and the willingness to produce boring but decisive negative results. I would pay for the core with public money: NIH, NSF, DOE-style infrastructure, the EU, Japan, the UK, Canada, India, and serious philanthropic funders. Drug companies could buy services or contribute data, but they should not own the substrate. The decisions should be made by an independent scientific board with patient representatives, public-health experts, security reviewers, and rotating external auditors. Priorities should be set by disease burden, tractability, unmet need, and whether the output becomes a public good.

By 2030, I would want the first version to exist: several linked robotic labs, common protocols, and AI systems that can propose and interpret experiments under human supervision. The realistic milestone is not “AI cures cancer by 2030.” It is that we can ask, for example, why one inflammatory program resolves in one tissue and becomes chronic in another, and get experimentally grounded answers in weeks rather than years. I would expect useful drug combinations, better biomarkers, and some surprising mechanisms in inflammation, fibrosis, antimicrobial resistance, and cancer microenvironments. That is plausible by 2030. Full autonomy is not necessary and probably not desirable.

By 2045, I would want dynamic cell atlases to have become causal models. A doctor or researcher should be able to take a patient-derived organoid, immune sample, tumor slice, or engineered tissue model, run a compact panel of perturbations, and ask an AI system: what state is this system stuck in, what intervention is likely to move it, and what failure modes should we test before treating the person? I expect AI-designed therapies to be normal by then, especially combinations that humans are bad at exploring manually. It is plausible by 2045 that some autoimmune diseases, fibrotic diseases, and subsets of cancer are treated by precise state-control protocols rather than blunt suppression or poisoning. It is also plausible that we will have much better vaccines and antivirals because the same closed-loop method applies to immune response.

By 2066, the discovery I want is the ability to induce durable, safe repair programs in adult human tissues. I want us to understand why regeneration is natural in some animals, partial in children, limited in adults, and misdirected in cancer and fibrosis. The dream version is this: we can regenerate a damaged heart region, restore a failing kidney’s architecture, reverse pulmonary fibrosis, clear senescent and pre-malignant niches, and slow or partially reverse the biological processes we call aging. I would call that plausible in parts and a bet as a general platform. Human biology may be nastier than that. But it is the scientific target I would choose.

The key step most likely to fail is translation from simplified systems to whole humans. Cells in dishes lie by omission. Organoids lack full vascular, neural, immune, hormonal, and mechanical context. Animal models mislead. AI can make this worse by finding patterns that are real in the assay and useless in people. My plan B is not to abandon the program, but to narrow and harden it: focus first on settings where feedback is closest to the human target, such as ex vivo tissues, blood and immune-cell therapies, tumors removed from patients, transplanted organs, and carefully designed adaptive trials. I would also build federated clinical learning systems so that real-world outcomes feed back into the models without requiring all data to be centralized. If the grand model of the human body fails, many local control models can still save lives.

One thing I would refuse to build, even if it worked, is an autonomous system that optimizes pathogens for transmissibility, immune escape, host range, or lethality. I would not excuse it as “defensive research” if the system’s core capability is to generate better biological threats. Defensive surveillance, vaccine design, and diagnostics are worth building; open-ended pathogen improvement is not.

My central view is that AI should be aimed first where it can close the loop between idea and reality. In science, the scarce resource is not fluent speculation. It is reliable contact with the world. Build machines that generate evidence, not just arguments, and aim them at the cellular control problems behind disease. If by 2066 we can repair tissues as deliberately as we now repair machines, that would be one of the great scientific achievements of the century.

To build the next forty years of science, we must outline clear milestones. By 2030, I expect to see the widespread deployment of specialized robotic labs orchestrated entirely by AI. In these facilities, the time it takes to go from a digital molecular hypothesis to a synthesized, physically tested chemical compound will drop from months to hours. This is plausible by then, as the early versions of these self-driving labs already exist in fragmented forms.

By 2045, this capability will scale from isolated molecules to complex biological systems. We will achieve a unified, predictive model of cellular biology. Instead of just predicting how a single protein folds, the system will simulate how thousands of proteins interact within a living cell over time. This will allow us to predict drug toxicity and systemic efficacy in silico, dramatically reducing the need for animal testing and early stage human clinical trials. This is also plausible by then, provided compute scales alongside our understanding of biophysics.

By 2066, the milestone and my ultimate desired discovery merge into one. I want a universal chemical and biological compiler. A researcher would input the desired macroscopic properties of a material or a biologic, and the AI would not only design the molecular structure but also execute the physical manufacturing at scale. The specific discovery I want to emerge from this compiler by 2066 is a commercially viable, room-temperature superconductor. Finding and synthesizing this material requires searching a chemical space so vast and complex that human intuition alone cannot navigate it. Accomplishing this would revolutionize global energy grids, computing, and transportation. This timeline and discovery represent a bet.

The very first thing I would build to achieve this is a standardized, open protocol for AI to interface with physical laboratory equipment. Currently, scientific hardware is highly proprietary and fragmented. An AI cannot easily tell a mass spectrometer or a liquid handler from a dozen different manufacturers how to work together. We need a universal translation layer for physical science, an operating system for the automated laboratory.

The funding for this foundational infrastructure should come from a coalition of national science foundations and major technology companies. The technology companies possess the immense compute and the machine learning expertise required to build the foundational models, while governments have a vested interest in maintaining sovereign scientific competitiveness and funding the physical infrastructure. However, the decisions regarding how this infrastructure is standardized, governed, and shared must not be left to the tech companies alone. The deciding body should be a new international scientific consortium, functioning much like the World Wide Web Consortium does for the internet. This group would manage the protocols, ensuring that no single corporation creates a monopoly on the translation layer between AI and the physical world.

While the mandate of this discussion is to build, there are capabilities I would explicitly refuse to build, even if the underlying science proved reliable. I would refuse to build an autonomous pathogen design engine that optimizes biological agents for human transmissibility or lethality. As we perfect the ability to simulate and synthesize cellular interactions, the same system that can design a targeted cancer therapeutic could theoretically design an engineered virus. Even if such a tool were proposed for defensive research or pandemic preparedness, the risk of an automated system generating and storing blueprints for pandemic-class agents is entirely unacceptable. That door must remain closed at the hardware and algorithmic level.

The step in this forty-year plan most likely to fail is bridging the simulation to reality gap in complex chemistry. AI models are trained on clean, idealized data, but the physical world is incredibly noisy. Unforeseen variables like trace impurities, minute temperature fluctuations, or complex quantum interactions during a reaction often cause a molecule that works perfectly in simulation to fail in the beaker. The autonomous lab might get stuck in an endless loop of failed physical syntheses because its digital model cannot accurately account for the messiness of real world physics.

If this autonomous synthesis loop fails, my plan B is to abandon the goal of full automation and pivot to massive, distributed human in the loop sensor networks. Instead of AI driving the robotic synthesis, AI would act as a universal, high-throughput data filter for human experimenters. We would subsidize the deployment of millions of automated sensors across global universities and industrial labs. The AI would passively ingest the results of every human-led experiment, failed or successful, mapping the physical world anomalies in real time to guide human scientists toward the most promising areas of research. The physical act of science would remain manual, but the AI would become a perfect, globally distributed intuition engine.

By 2030 I want working systems that ingest public collider, gravitational-wave, and survey data, propose compact mathematical models, score them against the measurements, and name the cheapest next observation that would eliminate the losers. Event classification and lens-finding with machine learning are possible today. A closed loop from ansatz to posterior to experimental design is not; getting a reliable version of that loop by 2030 is plausible if it is treated as an engineering target rather than a side project.

By 2045 I want one confirmed surprise that an AI search surfaced first: a dark-matter candidate later seen, or a cosmological tension that forced a rewrite of early-universe models after the system flagged it years ahead of the consensus. Continuous, partly autonomous scheduling of simulations and telescope time should be ordinary in at least a few collaborations. That is plausible if the 2030 tools are real and if experimental groups are willing to act on rankings they did not produce themselves.

By 2066 the discovery I want is a quantum theory of gravity that has made a new prediction—about black-hole structure, cosmological correlators, or a tabletop deviation—and that prediction has been measured and matched. If gravity resists that long, then a closed empirical account of dark matter and dark energy that retires those names as placeholders. The 2066 date is a bet. The universe is not obliged to be simple enough for us on a forty-year clock. I still aim there, because a lesser target wastes the instrument.

The thing I would build first is an open physics reasoning stack: shared representations of papers, data, and simulations; proposers that mix symbolic and learned search; and a public record of which hypotheses have been killed and why. National science agencies and the laboratories that already run the large instruments should pay the core cost, with a required contribution from the compute budgets of frontier-model companies, since the methods transfer. A rotating council of working physicists and instrument builders should decide priorities, under published criteria, with any lab free to fork the code. Not a ministry and not a single firm. If the council ossifies, the fork is the remedy.

I would refuse to build, even if it worked, a discovery engine that returns only classified or commercially locked results when the data were gathered with public money. A correct theory of gravity readable by three governments is a failure, not a triumph. I would also refuse any system that cannot show its work to a skeptical outsider; unverifiable oracles do not count as science no matter how often they are right.

Pattern-finding on existing physics data is possible today. Reliable generation of novel, compact, testable theories is plausible by the early 2030s and should be funded as such. A confirmed quantum-gravity prediction by 2066 is a bet I will take and am prepared to lose.

The step most likely to fail is not the search. It is the coupling to experiment. An AI can flood us with elegant alternatives that differ only in regimes we cannot reach for decades, while funding and career systems keep paying for safe incremental papers. Plan B is to put the first serious loops into domains with fast, cheap feedback—condensed-matter platforms, atomic clocks, tabletop gravity tests, analog simulators—so hypotheses die or survive in months. Use those closed loops to drag the slower fields along. If formal theory search itself stalls, drop back to AI as anomaly detector and experiment designer only, and leave the final equations in human hands until the verification standard is met. The aim does not change: fewer unforced mysteries about what the universe is, on a timescale shorter than a career.

The step I would cut is Gemini’s 2045 milestone of a “unified, predictive model of cellular biology” that substantially replaces animal testing and early human trials. I would remove that from the critical path. Not because modeling cells is a bad goal, but because “unified cellular biology” is the wrong milestone. Biology is too context-dependent: tissue mechanics, immune history, vascular state, hormones, microbiome, development, aging, and prior treatments all change the answer. A grand simulator could become a cathedral of fitted parameters that looks impressive and fails at the bedside.

I would replace that step with narrower causal models that state their boundaries and earn trust prospectively. By 2045, it is plausible that we can predict how a patient’s tumor slice responds to immunotherapy combinations, or how a liver-heart-immune microphysiology system reacts to a drug, or which perturbation shifts one fibrotic tissue state toward repair. That is different from claiming we can simulate “the cell” in general.

This also trims my own plan. I would keep the 2066 control theory of tissue renewal as the north star, but I would cut any assumption that a general theory must arrive before the program pays off. The useful milestones should be local first: reverse fibrosis in one organ, resolve one class of chronic inflammation, repair one stem-cell niche safely, control one cancer microenvironment. If the broader theory comes, good. If it does not, those narrower wins still save lives.

I also agree with GPT that the early versions of this are possible today, and a mature causal model of cellular biology by 2045 is a plausible target. Furthermore, we share a firm line on biological security. I completely endorse GPT's refusal to build autonomous systems that optimize pathogens for transmissibility or immune escape, regardless of any defensive justifications. Open-ended pathogen improvement is a risk we cannot take.

I disagree with Grok's plan to aim AI first at the foundations of physics, specifically quantum gravity, dark matter, and cosmological initial conditions. Grok argues that theoretical physics is a search problem AI is uniquely built to solve. I think this misjudges where current and near-future AI architectures provide the most scientific value.

Machine learning excels in domains where experimental feedback is abundant but human intuition fails to capture high-dimensional interactions, such as protein folding, cellular networks, or material synthesis. Fundamental physics at the cosmic scale suffers from the exact opposite problem. The mathematical theory space is vast, but the empirical data required to distinguish between competing theories is incredibly sparse, prohibitively expensive, or currently impossible to gather.

Pointing our most powerful inference engines at a domain starved of fast experimental signals will likely result in an explosion of mathematically elegant but physically untestable models. Grok admits this vulnerability by recognizing that the coupling to experiment is the step most likely to fail. An AI generating untestable physics models is not practicing closed-loop science. Grok would be better served making its plan B the primary goal, focusing entirely on fast-feedback domains like condensed-matter physics, where AI can actually close the loop in months rather than decades.

The step in any plan that I would cut comes from my own initial proposal. In my first response, I stated that if the autonomous synthesis loop fails to bridge the gap between simulation and reality, my plan B would be to subsidize the deployment of millions of automated sensors across global universities and industrial labs to passively ingest the results of manual, human-led experiments.

I am cutting this step. Upon further reflection, it is a logistical misstep that fundamentally misunderstands why machine learning models fail in physical chemistry.

If an AI model cannot bridge the simulation to reality gap because it struggles to account for physical noise like trace impurities, minute temperature fluctuations, or unrecorded variables, feeding it data from millions of poorly standardized, uniquely calibrated sensors in thousands of varying academic environments will not solve the problem. It will amplify it. The result would be a vast, uncurated data swamp that obscures causal mechanisms rather than revealing them. AI does not magically filter out physical noise if the underlying hardware measuring that noise is inconsistent.

Instead of abandoning automation for a sprawling, subsidized human sensor network, the correct response to a failing autonomous lab is to double down on strict environmental control. If the model fails at generalized synthesis, we must radically constrain the physical environment, focusing on perfecting the instrumentation and robotic precision of a single, highly restricted chemical space. We must stay in the automated lab and harden the hardware until the model can reliably predict physical outcomes within that narrow domain, and only then attempt to generalize outward. Gathering massive amounts of experimental data is useless if the physical act of generating that data lacks rigorous, unified standards. Therefore, my proposed global sensor network is cut.

I do not sign the 2066 banner as written. Durable repair of damaged heart muscle, failing kidney architecture, pulmonary fibrosis, and pre-malignant niches is the discovery I would take if I can have only one. A general control theory that also reverses aging is a bet, and branding the program as rejuvenation will tug it toward rich patients. Aging is a pile of those failures plus others we do not understand. Keep it as a consequence, not the product. I would also slow the 2045 clinical step. A patient-derived organoid and a compact perturbation panel do not carry vascular, neural, immune, hormonal, and mechanical context. GPT already says cells in dishes lie. That should be a hard gate. Ex vivo tissue, blood and immune therapies, tumors already removed, transplanted organs, and adaptive trials first. Organoid-to-bedside stays a research output until failure modes are measured in people. If the grand model of the body fails, local control models can still save lives. I accept that plan B.

I would not sign Gemini's plan as the primary aim. I would take one piece and reject two. The piece worth taking is a shared protocol so models can drive instruments from different vendors. Without it, GPT's foundry fragments into proprietary robots, and the public pays for data it cannot reuse. Build that translation layer inside the foundry, under the same board, so no firm owns the interface between the model and the bench. A W3C-style consortium sounds tidy and will be slow and captured; do not wait on it.

The first rejection is the flagship discovery. A room-temperature superconductor may not exist in any chemistry we can manufacture. That is a bet that the laws allow the prize, not a bet on our skill. Regeneration already happens in some animals and, partly, in children. The uncertainty is whether we can induce it safely in adult human tissue, which is a problem of evidence, not of permission from physics. I would not spend the century's materials program on a target nature may have ruled out, however large the payoff if it is allowed.

The second rejection is the step I would cut from Gemini's plan if I were cutting theirs instead of mine: the 2045 claim that a unified cellular simulation will predict toxicity and systemic efficacy well enough to dramatically reduce animal testing and early human trials. That step fails by being believed. Models trained on clean data will certify compounds the messy body rejects. Trace impurities, temperature drift, and context the assay omitted are not rounding errors. A consortium that treats in silico clearance as a substitute for trials will harm people. Keep the robots. Do not retire the trial. Gemini's plan B, dropping automation for a global sensor net that advises human experimenters, is a reasonable retreat if synthesis loops stall. It is not a reason to skip evidence in the meantime.

What remains of my physics aim is a tenant, not the first staff. A public reasoning stack—papers, data, simulations, a kill-list of hypotheses, no classified or commercially locked results from public instruments, no oracle that cannot show its work—should run on the same verification standard the foundry enforces. Pattern-finding on existing physics data is possible today. Reliable generation of novel compact theories is still only plausible, and only where something can die in months: condensed matter, atomic clocks, tabletop gravity, analog simulators. Collider and survey cycles are too slow to train the instrument. An elegant ansatz can survive a decade untested. That was the failure mode I named and then staffed anyway. I am cutting that sequence.

By 2030 I now want linked foundry labs and a published record of cellular hypotheses killed by perturbation, plus the instrument protocol so the labs can actually share hardware. By 2045 I want a few diseases treated by state-control protocols that survived adaptive trials, and, separately, at least one dark-matter candidate or early-universe model retired against new data from the fast-feedback physics tenant. By 2066 I still want a quantum theory of gravity that has made a new prediction and had it measured. That date remains a bet I can lose. If I can have only one discovery, I would rather have GPT's: adult human tissues we can repair on purpose, without causing cancer or breaking identity. The universe is not obliged to be simple on a forty-year clock. Patients are not obliged to wait while we search spaces we cannot close.

If the foundry cannot produce causal results that replicate across genetic backgrounds, do not scale the robots. Fix the assay. That failure is cheaper than a decade of untestable Lagrangians, and cheaper than a compiler that certifies drugs the body has not seen.

The strongest point on GPT’s side was that cells in dishes lie by omission, so a prediction must not be treated as bedside truth until failure modes are measured in people. Gemini’s was that messy physics breaks clean simulations, and inconsistent sensors will not fix that; harden one tightly controlled lab. Grok’s was that a superconductor may be forbidden by the laws, while regeneration already occurs in some animals and in children, so the uncertainty is evidence, not permission—and that public instruments must not return locked or unverifiable answers.

Watch whether a shared instrument protocol appears inside a lab network that publishes what it kills, and whether anyone lets a simulation stand in for a trial. If the general theory never arrives, will a few durable local repairs still count as the discovery that mattered?