The Hypothesis Trap

When Scientists Fall in Bad Love With Their Own Ideas

Approximately four decades ago, I became a witness in a scientific misconduct case. The charges had been brought by an international postdoc in the lab where I had also worked before moving on, and I cannot remember many of the details, except that my written testimony stated that I knew nothing. But I do remember, in the context of more recent high-profile cases, that the essence of the accusation then was the same as it is now: altering experimental data to support the ‘party line’.

The recent disruption to American science has been extensively documented. Given how deeply intertwined government research dollars are with the budget models for R1 universities and the large academic medical centers, it’s not surprising that those funds were chosen for their leverage, and that the consequence of their being in jeopardy will profoundly alter the course of pursuing Vannevar Bush’s version of the endless frontier.

But I want to explore a different question raised by that long-ago case. When I recall that the essence involved “altering data to support the party line,” I need to ask: whose party line was it? In that case, and in many since, the party line wasn’t imposed by some external authority. It was the PI’s own hypothesis, their pet theory, the idea they’d invested years in developing and defending. The fraud wasn’t about serving power—it was about rescuing a cherished belief from contradictory evidence.

This raises uncomfortable questions about how we organize biomedical research. The current system—hypothesis-driven projects led by individual PIs who develop deep attachments to specific ideas—contains structural flaws that push even honest scientists toward motivated reasoning and occasionally push the dishonest ones past the line into fraud.

The Romantic Model of Science

Our funding system enshrines a particular vision of how science works. A brilliant investigator conceives a hypothesis. They design clever experiments to test it. They write a compelling grant proposal. If funded, they spend 3-5 years testing their idea. Success means publishing papers that confirm the hypothesis, which leads to more grants to extend the work.

This model has romantic appeal. It positions the PI as the creative genius whose insight drives discovery. It makes science a battle of ideas where the best hypotheses prevail. It creates clear narratives: an investigator proposes a theory, designs experiments to test it, and demonstrates it is correct. This is how we teach science, how we write about it in popular accounts, how we celebrate it in awards and prizes.

The problem is that this romantic model creates precisely the conditions under which fraud becomes tempting and honest self-deception becomes nearly inevitable.

When Hypothesis Becomes One’s Identity

Here’s what happened in numerous misconduct cases from the 1980s onward: A researcher develops a hypothesis. It’s not just any hypothesis—it’s their hypothesis, the idea that defines their research program, the theory that distinguishes them from competitors. They build a laboratory around it, recruit students and postdocs to test it, and write grants that promise to extend it.

The hypothesis becomes their professional identity. Colleagues know them as “the person who works on that theory.” Graduate students join their lab specifically to work on that problem. Papers in high-impact journals describe their unique contribution. Tenure committees evaluate whether the hypothesis has generated sufficient publications. Grant review panels judge whether the approach is likely to continue producing results.

Then experiments start yielding contradictory data. Not every experiment—if every experiment failed, the researcher might abandon the hypothesis. However, when enough experiments yield ambiguous or contradictory results, the careful scientist should begin to question the core idea.

This is where the system’s design creates problems. Walking away from the hypothesis means walking away from professional identity, from grants that depend on that research program, from students and postdocs whose projects are built on that framework. It means admitting that years of work may have been directed toward the wrong question. It means watching competitors promote alternative theories.

The pressure isn’t external—nobody is ordering the researcher to maintain their hypothesis. The pressure is structural, built into how we organize careers and evaluate success. When your identity, your lab’s funding, and your scientific reputation all depend on a particular idea being correct, it takes extraordinary intellectual honesty to acknowledge that idea might be wrong.

On the Spectrum: From Delusion to Fraud

Most scientists don’t fabricate data. But many engage in practices that fall short of fraud while still distorting the scientific record. These practices stem from the same structural problem: excessive investment in a specific hypothesis.

Selective reporting occurs when experiments yielding inconvenient results are dismissed as “technical problems,” whereas experiments supporting the hypothesis are published. The researcher isn’t fabricating data—they’re making judgments about which data are “good.” But those judgments are biased by investment in the hypothesis.

Data massaging occurs when researchers make analytical decisions that favor their theory. Which outliers to exclude? How to set cutoffs? Which statistical tests to use? Each decision seems defensible individually, but collectively, they bias results toward the preferred outcome. Again, this isn’t fabrication—it’s motivated reasoning dressed up as methodological choice.

Hypothesis rescue manifests as increasingly elaborate explanations for why experiments that should have supported the theory failed. Maybe the conditions weren’t quite right. Maybe there’s an additional factor we didn’t control for. Maybe the effect is context-dependent. Some auxiliary hypotheses are legitimate scientific refinements. Others are epicycles added to save a failing theory.

Selective collaboration and citation appear when researchers preferentially cite papers supporting their view while ignoring contradictory work. They collaborate with scientists who share their hypothesis, while avoiding those who promote alternatives. This creates echo chambers where a contested theory looks like a consensus because the believers only talk to each other.

These practices aren’t fraud in the legal sense. They’re what happens when intelligent, well-meaning scientists become too invested in particular ideas. The investment doesn’t require conscious dishonesty—it just requires the normal human tendency to see what we expect to see, to value evidence confirming our beliefs more highly than evidence challenging them.

The Cases We Remember

The 1980s wave of misconduct cases illuminates this pattern. Take John Darsee at Harvard Medical School. His fraudulent cardiology research wasn’t random fabrication—it was data manufactured to support his ongoing research program. He was so invested in demonstrating that his approach worked that he fabricated results when experiments didn’t cooperate. His extraordinary productivity should have raised red flags, but it fit the romantic model: the brilliant investigator producing breakthrough after breakthrough.

The Baltimore affair involved Thereza Imanishi-Kari’s immunology data that Margot O’Toole couldn’t replicate. The decade-long controversy ended in 1996 when an appeals board cleared Imanishi-Kari of all misconduct charges. But the case revealed how competing interpretations of the same data can arise when different investigators bring different assumptions to their analysis, and how difficult it becomes to distinguish between legitimate scientific disagreement and potential misconduct when researchers are deeply invested in their theories.

Eric Poehlman’s obesity research fraud—falsifying data in 17 grant applications and 10 publications—followed the same pattern. He had a research program, a reputation, and a stream of funding dependent on showing that his hypotheses about aging and obesity were correct. When data didn’t cooperate, he made them cooperate.

The common thread isn’t that these individuals were uniquely evil. It’s that they were operating in a system where too much depended on specific hypotheses being correct. The same pressures that led them to commit fraud push others into questionable practices and drive everyone toward motivated reasoning.

The Structural Alternative: Team Science

Consider how differently science works in fields that have moved away from the PI-centered hypothesis-driven model.

Large-scale genomics operates with diverse teams interrogating datasets rather than testing specific hypotheses. The question isn’t “Is my theory correct?” but “What patterns exist in these data?” Multiple investigators with different backgrounds and biases analyze the same datasets. Results require replication across labs. The data-sharing infrastructure enables other groups to independently verify findings.

Nobody’s career depends on a specific gene being associated with a particular disease. If your analysis suggests gene X matters but another team’s analysis contradicts that, there’s no professional catastrophe. You’re contributing to collective understanding rather than defending personal theories.

The BRAIN Initiative that I helped launch during my tenure at NSF was designed in part to avoid the hypothesis trap. Rather than funding individual PIs to test specific theories about brain function, it funded tool development, data collection, and infrastructure that multiple investigators could use. The bet was that understanding the brain required comprehensive data and analytical capabilities, not just clever hypotheses.

This doesn’t eliminate all bias—researchers still have preferences about which tools to develop or which brain regions to map. But it reduces the intense personal investment in any particular theory about how the brain works. The focus shifts from testing hypotheses to building shared resources.

Particle physics has worked this way for decades. Nobody at CERN builds a career on predicting a specific particle will or won’t be found. The infrastructure supports collective inquiry. Results require consensus across large collaborations. Data are shared immediately. Multiple teams analyze the same detector output.

Can you imagine a particle physicist fabricating Higgs boson data? The system makes it nearly impossible—not because particle physicists are more ethical, but because the organizational structure distributes both credit and accountability across large teams working with shared data.

The Biomedical Research Counterfactual

What would biomedical research look like if we designed it to minimize the hypothesis trap?

Separation of hypothesis generation from testing. One team develops theories and predictions. A different team, with no stake in the theory’s success, conducts the experiments. The testing team is rewarded for rigorous methods and clear results, not for confirming or refuting specific hypotheses. This isn’t unprecedented—clinical trials often use this model, with statisticians who haven’t seen interim results conducting final analyses.

Registered reports and pre-registration. Require researchers to specify hypotheses, methods, and analyses before collecting data. Journals commit to publishing based on methodological quality, not results. This removes the temptation to massage data because publication is already guaranteed. The researcher benefits from doing careful work, not from obtaining specific results.

Adversarial collaboration. When competing theories exist, fund collaborations between proponents to design jointly agreed-upon decisive tests. Each side specifies in advance what results would falsify their theory. The collaboration is rewarded for clarity and rigor, not for one side winning.

Collective attribution and team leadership. Move away from the PI model toward team leadership with distributed authority. Make it normal for multiple investigators to share senior authorship without hierarchical ordering. Reward contributions to collective projects, not just defending personal theories. This reduces the intensity of individual investment in specific hypotheses.

Diverse parallel approaches. Rather than funding one investigator to test one hypothesis over five years, fund multiple teams to simultaneously test competing hypotheses. Make this explicit: “We think question X is important but don’t know which of three theories is correct, so we’re funding all three approaches.” The field benefits from comparative testing; individual investigators aren’t catastrophically invested in one answer.

The Objections

These suggestions will provoke immediate resistance, much of it justified. The romantic model of science—brilliant individual investigator pursuing visionary ideas—isn’t entirely fiction. Great insights do come from individuals. Breakthrough theories do require conviction to pursue against skepticism. Hypothesis-driven research has produced genuine discoveries.

Moreover, team science and collective approaches have their own challenges. Large collaborations can become bureaucratic. Consensus-building can delay needed action. Distributing credit across many people may reduce individual incentive for excellence. Pre-registration can be gamed by enrolling multiple studies and selectively reporting which ones to complete.

The adversarial collaboration model assumes good faith from competing investigators, which isn’t always present. Separating hypothesis generation from testing may slow progress if the best experiments require an intimate understanding of the theory. Distributed leadership creates coordination problems.

These are real concerns. I’m not arguing for the complete abandonment of hypothesis-driven research or the PI model. But I am arguing that we’ve over-indexed on one way of organizing science—a way that creates predictable problems around motivated reasoning and hypothesis attachment—without seriously considering alternatives that might mitigate those problems.

The Incentive Redesign

The deeper issue is incentive structure. We reward:

  • Publications in high-impact journals (which prefer dramatic confirmations of interesting hypotheses)
  • Grant funding (which requires convincing reviewers you’re pursuing important ideas likely to yield results)
  • Citations (which accumulate for papers making strong claims, not for careful null results)
  • Awards and prizes (which celebrate breakthroughs, not rigorous refutations)
  • Tenure and promotion (based on establishing an independent research program—meaning a distinctive hypothesis)

Each incentive encourages researchers to develop strong attachments to specific theories. The scientist who carefully tests a hypothesis, finds ambiguous results, and concludes, “This is more complicated than we thought,” doesn’t thrive under these incentives. The scientist who generates a provocative theory, designs experiments to support it, and publishes dramatic results thrives—even if the theory is ultimately wrong.

We could design different incentives:

  • Reward rigorous replication attempts
  • Fund adversarial collaborations that test competing theories
  • Celebrate careful negative results that prevent the field from pursuing dead ends
  • Promote scientists who change their minds when evidence demands it
  • Value contributions to infrastructure and methods that enable collective progress

None of this is unprecedented. Clinical trial statisticians build careers on methodological rigor, not therapeutic breakthroughs. Methods developers in genomics gain recognition for creating tools others use. Psychology researchers are valued for independently testing whether published findings hold up.

The question is whether biomedical research, more broadly, is willing to diversify its incentive structures and organizational models. The field is enormously successful—NIH funding, breakthrough therapeutics, extended lifespans. Why change a winning formula?

BACK TO THAT 1980S CASE

The postdoc who brought misconduct charges understood something important: when data are being altered to support “the party line,” someone needs to object. That takes courage—postdocs are vulnerable, whistleblowers face retaliation, and questioning senior scientists is risky.

But here’s what I’ve come to understand that I didn’t fully appreciate forty years ago: the party line wasn’t imposed from outside. It emerged from structural features of how we organize research. The PI who allegedly manipulated data wasn’t serving some external master. They were serving their own hypothesis, the idea they’d built a career around, the theory their lab existed to develop.

That makes the problem both worse and better than simple corruption. Worse, because it means well-meaning scientists with good intentions can slide into questionable practices without recognizing it. The same motivated reasoning that drives fraud also drives less dramatic but equally problematic biases in how we collect, analyze, and report data.

Better because it means organizational redesign might help. We can’t eliminate human fallibility or the emotional attachment scientists develop to their ideas. However, we can design systems that reduce the extent to which outcomes depend on any particular hypothesis being correct. We can create structures where admitting you were wrong is professionally survivable. We can reward rigor over drama, collective progress over individual breakthroughs.

The Path Forward

I’m not optimistic about radical transformation. The biomedical research enterprise is vast, successful, and institutionally entrenched. The romantic model of the lone investigator testing brilliant hypotheses is deeply embedded in how we tell science stories, train graduate students, and allocate prestige.

But incremental change is possible:

Funding agencies can require pre-registration for hypothesis-driven research while also funding more exploratory, team-based approaches. NIH’s BRAIN Initiative and precision medicine programs already point in this direction. Expanding these models would diversify how research gets organized.

Journals can mandate data sharing and the use of registered reports. Some journals already do this; others resist for fear of losing exciting submissions to competitors. But collective action could shift norms. If high-impact journals required rigorous transparency, researchers would adapt.

Universities can broaden tenure criteria to value methodological rigor, replication, infrastructure development, and collaborative contributions, alongside traditional metrics of independent research. This requires courage because it means promoting faculty who don’t fit the standard template, but it’s feasible.

Training programs can teach critical evaluation of one’s own hypotheses. Rather than just training students to design clever experiments and write compelling grants, we can teach them to actively look for ways they might be wrong, to value evidence against their theories, and to see changing one’s mind as a strength rather than a weakness. This is partly cultural, partly structural.

Funders can experiment with alternative models. Fund some research explicitly as adversarial collaboration. Fund some as team science with distributed leadership. Fund some as infrastructure development. Create parallel tracks so researchers can build careers through multiple pathways, reducing the pressure to develop intense attachment to specific hypotheses.

None of this will eliminate fraud—there will always be individuals who cheat. However, it might reduce the structural pressures that push honest scientists toward motivated reasoning and, in some cases, scientists toward outright fabrication.

Integrity is More Than Honesty

That 1980s case I barely remember continues to inform my thinking, not because I have clear memories of it but because it captures something essential: scientific integrity requires more than individual honesty. It requires organizational structures that don’t push even honest people toward biased reasoning.

The postdoc filing charges was practicing integrity. But they were fighting against a system where a PI’s attachment to their hypothesis created pressure—probably unconscious, probably rationalized, but pressure nonetheless—to make the data fit the theory. One brave postdoc can’t fix structural problems alone.

We’ve built an enormously productive research enterprise. Biomedical science has achieved genuine miracles. The hypothesis-driven, PI-centered model has generated breakthrough after breakthrough. I’m not arguing it’s failed—clearly it hasn’t.

However, I argue it’s flawed in predictable ways. The same features that make it successful—individual investigators developing strong convictions about important ideas and pursuing them relentlessly—also create conditions for motivated reasoning, questionable research practices, and occasional fraud.

Acknowledging those flaws doesn’t diminish the achievements. It opens space for experimentation with alternative models that might reduce the problematic incentives while preserving the creative energy that drives discovery. The question is whether we’re willing to diversify how we organize research or whether we’ll continue over-relying on a single model because it’s familiar and has worked in the past.

The endless frontier that Vannevar Bush envisioned shouldn’t be endless in just one direction. It should include exploring different ways of pursuing knowledge, different structures for organizing inquiry, and different incentives for rewarding contributions to collective understanding.

That’s the real challenge: not just preventing fraud but creating systems where the pressures toward fraud—and toward less dramatic but equally problematic biases—are reduced. Where changing your mind based on evidence is professionally rewarded rather than punished. Where attachment to ideas is balanced by commitment to collective truth-seeking.

The party line that worries me most isn’t imposed by political power. It’s the party line we impose on ourselves when we become too attached to our own hypotheses, when our professional identities become too entangled with specific theories, when the systems we’ve built make admitting error too costly. We need to extend that understanding to object not only to individual fraud but also to organizational structures that make such fraud more likely. Building not just oversight systems but alternative models of how to pursue science.

That’s the integrity challenge for the next forty years.

When Agencies Collaborate: What EEID Teaches Us About Pandemic Preparedness

The research team moved carefully through the forest canopy platform at dusk, nets ready. In Gabon and the Republic of Congo during the mid-2000s, international ecologists were hunting for the reservoir host of Ebola virus. They targeted fruit bat colonies—hammer-headed bats, Franquet’s epauletted bats, little collared fruit bats—collecting blood samples and oral swabs.

By December 2005, they had their answer, published in Nature. They’d found Ebola RNA and antibodies in three species of fruit bats across Central Africa. For years, scientists had known Ebola emerged periodically, but couldn’t identify where the virus persisted between human epidemics. This research provided the answer: fruit bats, widely distributed and increasingly in contact with humans as deforestation pushed people deeper into forests.

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That discovery triggered a wave of follow-up research, much of it funded through the Ecology and Evolution of Infectious Diseases program—EEID—a joint NSF-NIH-USDA initiative I would later help oversee. EEID-funded teams documented how human activities created spillover opportunities: bushmeat hunting, agricultural expansion into bat habitat, mining operations bringing workers into forests. They identified cultural practices that facilitated transmission: burial traditions, preparation of bushmeat, children playing with dead animals. They built mathematical models of how Ebola moved from bats to humans and then through human populations. The science showed where Ebola lived, how it spilled over, and which human behaviors created risk.

Yet nine years after that initial Nature paper—after years of EEID-funded research mapping Ebola ecology—the virus emerged in Guinea in late 2013 and was identified in March 2014. A two-year-old boy, likely exposed through contact with bats, became patient zero. Within months, the outbreak had spread to Liberia and Sierra Leone. By 2016, more than 28,000 people were infected and 11,000 died. The economic impact exceeded $2.8 billion.

I was leading NSF’s Biological Sciences Directorate at the time, overseeing NSF’s role in EEID. We had funded years of follow-up research. We knew fruit bats harbored Ebola. We had models for predicting transmission. We had mapped high-risk regions. And yet 11,000 people died anyway. All of this was foreshadowing what would happen with SARS-CoV-2 later and on a much larger scale.

Here is the uncomfortable question I’ve been wrestling with ever since: If we funded the right science and had years of warning, why were we not better prepared?

What EEID Was Supposed to Do

EEID launched in 2000 because infectious disease ecology fell between agency missions. NSF supported ecology but wasn’t focused on disease. NIH funded disease research but wasn’t equipped for field ecology. USDA cared about agricultural diseases but not the broader ecological context. The program brought all three together: NSF’s ecological expertise, NIH’s disease knowledge, and USDA’s understanding of agricultural-wildlife interfaces.

The administrative structure was elegant on paper. All proposals submitted through NSF underwent joint review by all three agencies, and then any agency could fund meritorious proposals based on mission fit. For Ebola research, this meant NSF might fund the bat ecology, NIH’s Fogarty International Center might support the human health surveillance component, and USDA might fund work on bushmeat practices—different pieces of the same puzzle, coordinated through a single program.

The program typically made 6-10 awards per year, totaling $15-25 million across agencies. Not huge money, but enough to support interdisciplinary teams working across continents. And it worked—EEID funded excellent science at the intersection of ecology and disease that no single agency could have supported alone.

Why Interagency Collaboration Is Genuinely Hard

When I arrived at NSF in 2014 with the outbreak at its peak, I inherited EEID oversight and quickly discovered that elegant-on-paper doesn’t mean easy-in-practice. The deepest challenges weren’t administrative—they were cultural.

NSF and NIH approach science from fundamentally different starting points. NSF’s mission is discovery-driven basic research. When NSF reviewers evaluate proposals, they ask: Is this important science? Will it advance the field? NIH’s mission is health-focused and translational. NIH reviewers want to know: Will this help prevent or treat disease? What’s the public health significance?

I saw this play out in a particularly contentious panel meeting around 2016. Our panelists were reviewing a proposal on rodent-borne hantaviruses in the southwestern U.S.—excellent ecology, good epidemiology, solid modeling. The NSF reviewers loved it: beautiful natural history, important insights about how environmental variability affects transmission. The NIH reviewers were skeptical: where was the preliminary data on human infection? How would this lead to intervention?

An hour passed debating what constituted “good preliminary data.” For NSF reviewers, the PI’s previous work establishing field sites was sufficient—it showed feasibility. NIH reviewers wanted preliminary data on the virus itself, on infection rates. They weren’t being unreasonable—they were applying NIH’s standards. But we were talking past each other.

That debate crystallized the challenge. Two agencies with different cultures had to agree on the same proposals. Sometimes it created productive tension. Sometimes it just meant frustration.

The administrative burden on investigators was worse than we acknowledged. When NIH selected a proposal for funding instead of NSF, the PI had to completely reformat everything for NIH’s system—different page limits, different budget structures, different reporting requirements. This could add 3-6 months to award start dates. Try explaining to a collaborator in Guinea why you don’t know which U.S. agency will fund your project or when you’ll actually get money.

For program officers, EEID meant constant coordination overhead—meetings to discuss priorities, coordinating review panel schedules across agencies, negotiating which agency would fund which proposals. This work wasn’t counted in official program costs, but it was real. Hours we could have spent on other portfolio management.

Despite all this friction, EEID succeeded at its core mission. It funded research that advanced both fundamental science and disease understanding. When the 2014 Ebola outbreak hit, epidemiologists reached for transmission models developed through EEID grants. The program had trained a generation of researchers in genuinely interdisciplinary work.

What the 2014 Outbreak Exposed

But here’s what haunts me: we funded the science but not the systems. By 2014, nearly a decade of research had confirmed fruit bats as Ebola reservoirs, mapped their distribution across Africa, and identified high-risk human-bat contact zones. Papers were published in top journals. And then… nothing. No one built surveillance systems in West African villages where contact with bats was common. No one established early warning networks. No one created mechanisms to translate “we found Ebola in these bats” into “we’re monitoring for spillover in Guinea.”

EEID funded research, not surveillance. That’s appropriate—it’s a research program, not an operational public health system. But there was no mechanism to bridge the gap. When EEID-funded scientists discovered important findings, those findings stayed in academic papers. They didn’t flow to CDC, didn’t trigger surveillance efforts, didn’t inform preparedness planning.

During our quarterly coordination calls with NIH and USDA program officers, the question would occasionally arise: Who’s responsible for acting on what we’re learning? If EEID research identifies high-risk pathogen reservoirs, whose job is it to establish surveillance? The answer was usually silence, then acknowledgment that it wasn’t our job—we fund research—but uncertainty about whose job it was.

The missing infrastructure was organizational, not intellectual. We knew enough to be better prepared. The problem was lack of systems to act on knowledge. No agency was responsible for translating academic research into surveillance systems. CDC focuses on domestic diseases. NIH funds research but doesn’t run operations overseas. USAID’s PREDICT program did fund surveillance but didn’t have coverage in Guinea. We had pieces of the puzzle but no mechanism to assemble them.

I remember discussions about whether EEID should become more operational—perhaps requiring funded projects to include surveillance components. The response was always that this would fundamentally change the program’s character. NSF resists mission-directed research. My former agency’s strength is supporting investigator-driven discovery. Making EEID operational would require multiple agencies and authorities, and, most importantly, substantially more funding. A research program can’t solve an operational preparedness gap.

The scale problem was obvious. At $15- $ 25 million per year, EEID could support excellent science but not comprehensive surveillance. Think about what that would require: ongoing monitoring in multiple countries, relationships with local health systems, rapid response capacity, and laboratory infrastructure. This requires hundreds of millions annually, not tens of millions.

The timeline mismatch was equally frustrating. Research operates on slow timescales—EEID grants ran five years, and from proposal to publication might take 6-7 years. The initial bat reservoir discovery was published in 2005. If that had immediately triggered surveillance in West Africa, we’d have had nearly nine years before the 2014 outbreak. But triggering surveillance takes decisions, funding, international coordination—processes that themselves take years. By the time anyone might have acted, attention had moved elsewhere.

What This Means for Pandemic Preparedness

The most troubling insight: we knew enough to be better prepared for Ebola, and later for COVID-19, but knowledge alone wasn’t enough. EEID succeeds at advancing knowledge but can’t create surveillance systems, can’t fund operational preparedness, can’t bridge the gap between discovering threats and preventing epidemics. That gap is organizational and political, not scientific.

Should we expand EEID? More funding would support more projects, but it wouldn’t solve the fundamental problem. You could triple EEID’s budget and still have the research-to-surveillance gap. More papers about bat reservoirs don’t automatically create early warning systems. The limitation isn’t insufficient research funding—it’s absence of operational systems to act on research findings.

We need something structurally different. Here’s what I’d do:

First, create a rapid-response funding mechanism within EEID. When Ebola emerged in 2014, imagine if researchers could have gotten funding within weeks to investigate transmission dynamics and surveillance in surrounding regions, rather than waiting for the next annual competition. Model this on NSF’s RAPID program—streamlined review, modest awards ($100-200K for one year), quick deployment—but create an entirely different pocket of money for it from all the participating funders.

Second, establish formal connections between EEID and operational agencies. This is the biggest gap. Require EEID-funded researchers to submit one-page “surveillance implications” memos with final reports, which program officers share with CDC, USAID, and WHO. Better yet, have CDC or BARDA co-fund some EEID proposals with clear surveillance applications. Create visiting scholar programs where CDC epidemiologists spend time with EEID research teams and vice versa.

Third, strengthen international partnerships with genuine co-leadership. The 2014 outbreak showed the cost of inadequate surveillance infrastructure in West Africa. Expand EEID to include more disease hotspot regions—India, Brazil, Indonesia, DRC, West African nations—where foreign investigators can be lead PIs, foreign institutions receive and administer funds, and research priorities reflect host country needs. This isn’t altruism—it’s pragmatic self-interest.

The Larger Lesson

Interagency collaboration is genuinely hard—the friction I described isn’t fixable through better management. It’s inherent when bringing together organizations with different missions and cultures. EEID proves such collaboration can work and produce excellent science. But it requires sustained effort, goodwill, and tolerance for complexity.

The alternative—each agency in its silo—is worse. Infectious disease ecology requires expertise no single agency possesses. Complex problems require complex solutions. EEID demonstrated this is possible. The challenge is making it sufficient.

What haunts me is that we’re probably going to repeat the pattern. Right now, post-COVID, pandemic preparedness has political salience. But history suggests this won’t last. After the 2014-2016 Ebola outbreak, there was similar urgency. Within a few years, budgets declined and attention shifted. USAID’s PREDICT program was terminated in 2019—just months before COVID—due to budget constraints. We cut surveillance funding during a quiet period, then paid an enormous price when the next pandemic hit.

Prevention is invisible. We never know which pandemics we successfully prevented. There’s no constituency defending preparedness funding when cuts loom. That’s the structural problem we haven’t solved.

What Needs to Happen

Will we learn from EEID’s experience and build the infrastructure we need? Or will we fund the right research but lack systems to act on it—again?

The answer depends on recognizing that pandemic preparedness isn’t primarily a scientific challenge—we know enough—but an organizational and political one. Can we create structures spanning research and operations? Can we sustain funding between crises? Can we build systems robust enough to survive political leadership changes?

EEID succeeded at what a research program can do: funding excellent science that advanced understanding. The larger failure—inadequate pandemic preparedness—requires solutions at different organizational levels. But EEID’s experience provides a foundation: proof that interagency collaboration can work, that we can identify threats before they become catastrophes.

The team in Central African forests collecting bat samples did their job. They found the virus, mapped the threat, advanced our understanding. The question for the rest of us—program officers, policymakers, public health officials, citizens who fund this through taxes—is whether we’ll do our job: building systems that turn knowledge into prevention.

Science can identify threats. But preventing pandemics requires more than science. It requires sustained organizational commitment, interagency coordination, international cooperation, and political will—especially during quiet periods when threats seem distant. EEID demonstrated the scientific component is feasible.

The rest is up to us. And based on what I’ve seen, I’m not optimistic we’ll get it right before the next one hits.

Three Things Aviation Teaches Us About Science Funding

A trip to Long Beach Airport reveals something deep about policy

The LA Uber driver let me off at the small passenger terminal at Long Beach Airport, and I had to do some serious trial and error with Google Maps to find the old Douglas Aircraft hangar where JetZero had set up shop with the admirable goal of completely disrupting the commercial aviation market by building a wide-body blended wing aircraft that would carry a 787 Dreamliner load of passengers across the country for half the fuel cost.

The hangar was open to the air, the ramp and runway fully active, yet the ethos inside was pure early-2000s Google—when anything seemed possible. The enormous space was filled with a full-size cabin mock-up, engineers at workstations, cinema-size screens streaming CAD imagery of the new plane sporting various well-known airline liveries, and a collection of flying scale model drones. The plane itself looked like it had flown off a science fiction set.

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The engineering team was equally striking: veterans from Boeing, Embraer, and McDonnell Douglas, each bringing decades of experience from very different aviation cultures. I met one of the chief designers—the inventor of sharklets, those forked wingtips that reduce drag and improve fuel efficiency, now ubiquitous on some commercial aircraft. Another engineer had come from Embraer, where he’d designed the popular 2×2 cabin configuration that passengers overwhelmingly prefer on narrow-body aircraft. Now he was tackling the challenge of designing a completely new kind of airplane cabin that would maximize comfort in a blended wing configuration.

These engineers had learned their craft in established organizations with very different approaches to decision-making, risk assessment, and innovation. The wave of consolidation in aviation—most notably Boeing’s merger with McDonnell Douglas and its subsequent shift from an engineer-driven culture to one focused on shareholder returns—had left many veteran engineers looking for something different. The 737 MAX crisis highlighted how far Boeing had drifted from its engineering roots. JetZero represented a chance to get back to what they loved: solving hard technical problems without the constraints of quarterly earnings calls and legacy infrastructure.

They were attempting something none of their former employers would touch: a radical departure from the tube-and-wing design that has dominated commercial aviation for seventy years. This raised a question that goes far beyond aircraft design: Why can radical innovation happen at a startup like JetZero but not at Boeing, Airbus, or Embraer?

This isn’t just about airplanes. It’s about how organizations—whether aircraft manufacturers or science funding agencies—decide what’s worth building, who gets to decide, and how they balance proven approaches against risky bets. Aviation and science funding face the same fundamental challenge: how to organize technical innovation.

Studying how Boeing, Airbus, and Embraer make these decisions has revealed patterns that apply directly to science funding. Here are three lessons from aviation that illuminate how research gets funded—and why some innovations happen while others never get off the ground.

Lesson 1: How Organizations Assess and Manage Technical Risk

The Aviation Pattern

Boeing, in its traditional engineer-driven culture, approached risk through data and testing. Engineers made decisions based on technical feasibility. They’d prove something worked, then seek regulatory approval. The 787 Dreamliner exemplified this: Boeing pushed carbon-composite technology to unprecedented levels while keeping the basic configuration conventional. The cultural assumption: engineers know best, prove it works, get approval, move forward.

Airbus operates from a completely different framework. As a consortium involving multiple governments, labor unions, and industry stakeholders, risk assessment includes political, economic, and social factors alongside technical ones. Workers’ councils have a voice in production decisions. Safety regulators participate earlier in the design process. The A380 Superjumbo was technically conservative—four engines, conventional configuration—but represented enormous manufacturing and political risks, requiring coordination across nations. The cultural assumption: technical decisions affect many stakeholders, and all deserve input.

Embraer’s approach reflects its position as a state development tool for Brazil (the country holds a veto over control of the company’s strategic direction). They can’t compete head-to-head with Boeing and Airbus, so their risk calculus focuses on market positioning. Find niches, develop partnerships, move quickly. The E-Jet family succeeded by targeting the underserved regional market. The cultural assumption: innovation means finding white space in a market dominated by established players.

Same engineering principles. Same physics. The same goal of building safe, efficient aircraft. But fundamentally different risk assessment frameworks.

The Parallel to Science Funding

The American system, through NSF and NIH, operates remarkably like Boeing’s traditional approach. Peer review is engineer-driven decision-making translated to science. Data—preliminary results, track record—drives decisions. The central question reviewers ask is Boeing’s question: “Can this PI deliver with taxpayer money?” Merit review happens after the proposal is submitted. The system rewards incremental progress from established investigators, just as Boeing refined the 737 through successive iterations.

European research funding embeds more stakeholder involvement. Horizon Europe’s missions approach brings policymakers, industry representatives, and public voices into the priority-setting process. Risk assessment explicitly includes societal benefit and economic impact. Clinical translation gets emphasized earlier in the research pipeline. Scientists remain central but aren’t the sole decision-makers.

Emerging science powers like China take yet another approach. Strategic national priorities drive funding decisions. The question isn’t “What’s the best science?” but “Where can we compete globally?” This enables leapfrog strategies: massive focused investments in AI, quantum computing, and biotechnology designed to establish leadership in emerging fields rather than catching up in established ones. This top-down approach is now also emerging within the US science ecosystem.

For researchers, understanding which risk framework you’re operating in helps you frame proposals effectively. The American system rewards demonstrated competence and incremental progress. Other systems may value societal impact, strategic positioning, or rapid deployment. Neither approach is better or worse—they reflect different cultural assumptions about how to allocate risk in technical innovation.

Lesson 2: Who Gets to Decide What Gets Built

The Aviation Pattern

At Boeing, engineers and program managers traditionally drove major decisions. Shareholders and the board provided financial constraints. Airlines shaped requirements. But core technical choices were the engineers’ responsibility. This produced technically sophisticated aircraft, sometimes disconnected from market realities. The 747-8 (the last of the classic jumbo jets’ instantiations), for instance, was an engineer’s dream—but the market for it was lukewarm.

Airbus engages multiple stakeholders from day one. National governments in France, Germany, the UK, and Spain have seats at the table. Workers’ councils negotiate production methods. Industry partners across Europe collaborate on components. Customers get involved earlier. The result is more consensus-driven and sometimes slower, but with broader buy-in. The A350’s long development process reflected extensive consultation but yielded strong market acceptance.

Embraer’s alignment with Brazil’s government development goals sets direction, but the company maintains a partnership model with established players and responds quickly to market signals. Less hierarchical decision-making enables nimble adaptation. The attempted Embraer-Boeing partnership that ultimately fell apart illustrated starkly different decision-making speeds between the two companies.

JetZero represents something different entirely. A small team iterates rapidly. Engineers from different aviation cultures bring different assumptions. Venture capital’s risk tolerance differs fundamentally from corporate risk aversion. They can attempt radical innovation precisely because they’re not constrained by established stakeholder expectations or legacy infrastructure.

The Parallel to Science Funding

American peer review puts scientists in the decision-making seat. On its face, this seems ideal: who better to judge scientific merit than other scientists? But peer review favors known researchers using proven methods. Peers can become conservative gatekeepers. The result is high quality and incremental progress, but potentially missed breakthroughs.

European models bring more voices into the room. The European Research Council maintains scientific independence but operates within frameworks emphasizing societal missions and grand challenges. Policymakers, industry representatives, and public stakeholders help set priorities. Scientists remain central but aren’t the sole arbiters. This creates stronger connections to societal needs, though sometimes at the cost of researcher autonomy.

Directed research models flip the equation. Governments or funding agencies set priorities; researchers respond to calls for proposals. This is top-down rather than bottom-up. The advantage is alignment with national priorities. The risk is missing unexpected discoveries that don’t fit predetermined categories.

I’ve seen these differences firsthand, reviewing for both American and international funding agencies. The questions panels ask reveal cultural assumptions about whose judgment matters. American panels debate scientific rigor and PI capability. International panels I’ve participated in spend more time on broadening participation and strategic fit with national priorities.

For researchers, understanding who has a voice in funding decisions is crucial for navigating the system. American researchers working internationally need to recognize that peer review isn’t universal—other countries organize scientific decision-making to reflect different values about expertise, accountability, and public benefit.

Lesson 3: The Tension Between Incremental Improvement and Radical Innovation

The Aviation Pattern

Established aircraft manufacturers favor incremental improvement for sound reasons. The tube-and-wing design has been refined for seventy years. Every iteration builds on accumulated knowledge. Existing manufacturing facilities, pilot training programs, maintenance infrastructure, and regulatory pathways all assume this configuration. Airlines understand the operating economics. Risk is manageable, returns are predictable. The 737 MAX—an incremental update to a 1960s design—still makes economic sense despite its troubles.

JetZero’s blended wing body has been studied since the 1940s. Its technical advantages are clear: dramatic improvements in fuel efficiency, reduced noise, and potential for entirely new cabin configurations. But it requires new manufacturing processes, new pilot training, and new regulatory frameworks. The risk isn’t primarily technical—it’s organizational and systemic. There’s no clear path from prototype to profitable, scalable production. Established players, accountable to shareholders and constrained by quarterly earnings expectations, can’t justify the investment.

Startups like JetZero can attempt radical innovation because they have no legacy infrastructure to protect. They can accept higher technical risk. The venture capital model tolerates failure in ways public corporations cannot. They don’t need to satisfy existing stakeholders or worry about cannibalizing current product lines. They can focus on long-term disruption rather than next quarter’s earnings.

But we should be clear: most aviation innovation is incremental for good reason. Lives depend on safety. Capital requirements are enormous. Development timelines span 10-15 years. Regulatory burden is intense. Incremental improvement has delivered extraordinary gains—modern aircraft are unimaginably more efficient, safe, and capable than those of fifty years ago.

The Parallel to Science Funding

Science funding faces the same tension. Established PIs using proven methods dominate for sound reasons. Track records reduce risk. Incremental progress is predictable, publishable, and fundable. Infrastructure investments favor established approaches—if your university has a state-of-the-art imaging facility, proposals that use it have an advantage. Peer reviewers understand and can evaluate proven methods. The “preliminary data” requirement inherently favors ongoing work over genuinely new directions. The system is designed to minimize taxpayer waste through careful risk management.

Truly novel approaches struggle in this environment. High-risk/high-reward programs exist but represent a tiny fraction of overall funding. Early career investigators face a chicken-and-egg problem: “How will you do this?” reviewers ask, but gathering preliminary data requires resources they don’t yet have. Reviewers are more comfortable funding known quantities. Paradigm shifts are rare and unpredictable—there’s no clear “return on investment” for genuinely radical ideas.

Consider the BRAIN Initiative. The vision was bold: transform neuroscience through new technologies and approaches. But implementation favored established neuroscientists with proven track records. The system worked as designed: minimizing risk by funding demonstrated competence. As I’ve written earlier, BRAIN fell short in its delivery goals: curing brain diseases. ARPA-H was explicitly created to escape the incremental trap, but it’s still finding its model. The European Research Council’s advanced grants show somewhat higher tolerance for risk, but even there, track record matters enormously.

For researchers pursuing truly novel approaches, it’s crucial to understand you’re working against system design, not just reviewer bias. The system is optimized for reliable incremental progress, not moonshots. Radical innovation in science, like radical innovation in aviation, may require different funding models—something more like venture capital, tolerant of high failure rates in pursuit of occasional transformative breakthroughs.

This raises a deeper question: Should science funding favor incremental or radical innovation? Or do we need both, in different proportions? Aviation supports both Boeing’s incremental refinements and JetZero’s radical rethinking. Should science funding do the same—and if so, in what balance?

What This Means for Science Policy

These aviation patterns reveal a fundamental feature of how societies organize technical innovation. The choices Boeing, Airbus, and Embraer make about risk assessment, decision-making authority, and the balance between incremental and radical innovation aren’t purely business decisions. They’re cultural choices embedded in what Sheila Jasanoff calls civic epistemologies—different assumptions about how knowledge should be produced, who should decide, and what goals matter most.

American science funding has historically reflected American cultural values: individual merit and achievement drive peer review by scientific peers. Data-driven decision-making shows up in preliminary data requirements. Risk minimization operates through proven track records. Incremental progress represents the reliable path. This isn’t accidental—it’s deeply cultural.

Other countries organize differently because they value different things. European systems emphasize societal benefit and stakeholder input. Asian systems prioritize strategic national development goals. Different countries strike different balances between discovery and application, between researcher autonomy and national priorities, between tolerance for failure and demands for accountability.

For all researchers, understanding these cultural patterns helps you work more effectively within the system. Know what the system optimizes for—reliable incremental progress from established investigators. If you’re pursuing radical innovation, recognize you’re working against the grain. International collaborations require understanding that your partners may operate within fundamentally different funding cultures with different assumptions about what science is for and how it should be organized.

For science policy, we should be explicit about what our funding systems optimize for. There’s no “best” system—only different tradeoffs reflecting different values. Maybe we need multiple models, as aviation has both Boeing and JetZero. Comparing systems reveals assumptions we don’t normally question.

In future posts, I’ll explore specific country comparisons: How does the European Research Council actually work? What can we learn from how other countries fund AI research? How do different countries handle the tension between researcher autonomy and national priorities?

A Final Thought

Visiting JetZero and seeing engineers from Boeing, Embraer, and McDonnell Douglas collaborate on something radical that couldn’t happen within their former companies crystallized something I’d been observing in science policy work: innovation doesn’t just require good ideas and talented people. It requires organizational structures and cultural assumptions that allow certain kinds of ideas to be pursued.

The JetZero engineers didn’t suddenly become more creative or capable. They remained the same engineers who’d designed sharklets at Boeing or cabin configurations at Embraer. What changed was the organizational context—the risk tolerance, decision-making authority, and freedom from legacy constraints. That shift in context enabled them to attempt what had been impossible in their former roles.

Science funding works the same way. Researchers operating within NSF’s peer review system are no less creative than those pursuing radical ideas through ARPA or venture-backed biotechs. But the organizational context shapes which ideas can be pursued and which innovations are possible.

Understanding how different countries organize technical innovation—whether building aircraft or funding research—helps us see our own system more clearly. And maybe, just maybe, it helps us imagine how we might do things differently.

What examples have you seen where organizational culture shaped what research got pursued? Have you experienced different funding cultures working internationally? Share in the comments.

A Grant Reviewer’s New Year Advice to Proposers: What I’d Tell My Younger Self

Happy New Year! Below is Science Policy Insider’s first posting of 2026:

We were reviewing a proposal that included gorgeous preliminary data and confocal microscopy images from what was, at the time, cutting-edge: two-channel laser-scanning technology. Because the images were both crisply in focus and colored in green and red to reflect the locations of different sub-cellular fluorescent molecular probes, it felt as if this was an extraordinary grant proposal, based on the images themselves, never mind the fact that there was no working hypothesis nor technical consideration of a phenomenon called autofluorescence, where the biomolecules of the cell itself produce their own signal that can be confused with the signals coming from the two probes.

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The panel discussion revealed the problem. Some reviewers were ready to fund based solely on the images. Others raised the autofluorescence issue, the missing hypothesis. But even the skeptics prefaced their concerns with “The data are beautiful, but…” Those pictures had done their job—they made weak science look compelling.

That’s when I learned: awesome preliminary data can cloud objectivity. After reviewing thousands of grants at NIH and NSF over three decades, I’ve seen it happen repeatedly.

So, as you plan your 2026 submissions, here’s what I wish I’d known from the start—lessons that might save you the same learning curve.

Lesson 1: Clarity Beats Cleverness

In my early days, I thought impressive vocabulary and complex sentences demonstrated sophistication. Surely reviewers would appreciate nuanced, academic writing that showcased the full complexity of my thinking. I was wrong.

Clarity wins every time. Reviewers are overwhelmed, often reading up to 15 proposals a week while managing their own labs, teaching loads, and grant deadlines. Simple, direct writing isn’t dumbing down your science—it’s respecting your reviewers’ cognitive bandwidth and making your research accessible to the non-specialists who might be reading it.

Several decades ago, I learned the “grandmother” test. If you can’t explain your research clearly and simply to someone outside your immediate field (like maybe your grandmom), it’s probably not clear enough for a review panel where only one or two people are genuine specialists in your exact area.

Here’s my practical advice: Read your overall proposal goals (or aims) out loud. If you stumble over your own sentences, reviewers will too. Remember that if you can’t explain it, you probably don’t understand it well enough yourself. Make the first paragraph of each section a roadmap for what follows. And use jargon only when necessary—when there’s genuinely no more straightforward way to say it.

I once reviewed a proposal with brilliant research that was nearly incomprehensible to anyone outside the PI’s subspecialty. The same panel reviewed another proposal that explained equally complex ideas with straightforward language. Guess which one got funded?

Lesson 2: Preliminary Data Is About Trust, Not Volume

Early in my career, I believed more data equaled a stronger proposal. Fill those pages with figures! Show them everything you’ve got! Every additional graph strengthens your case, right?

Wrong. It’s the quality of the data that counts.

Here’s what preliminary data does: it answers the question “Can this PI execute what they’re proposing?” It’s not about impressing reviewers with how much you’ve already accomplished. It’s about building trust that you can deliver on your promises. And here’s the thing that surprised me most: including the wrong preliminary data raises more questions than having no data at all.

Show that you can execute the specific methods you’re proposing. Demonstrate the feasibility of your key innovation—the part that’s novel and risky. If you don’t have the correct preliminary data yet, address that gap head-on rather than papering over it with tangentially related work.

The deeper insight here is that reviewers are assessing risk. They’re not asking, “Do you have data?” They’re asking, “Do I trust you can deliver what you’re promising with taxpayer money?” Those are fundamentally different questions.

Lesson 3: Broader Impacts Require Situational Awareness

I initially treated broader impacts as a required checkbox. Standard language about societal benefits and outreach seemed perfectly adequate—everyone writes similar things, right? Just describe some plausible activities and move on.

Reviewers can spot boilerplate instantly. We’ve read hundreds of proposals with identical broader impacts sections, and they all blur together into meaningless noise.

The best broader impacts sections connect to who you are and what you’re genuinely already doing in ways that align with the nation’s best interests. Integration with your research and your actual life matters far more than ambitious plans that sound good on paper.

Scaling is essential: build on what you’re already doing rather than inventing entirely new programs you’ll never have time to implement. Be specific rather than grandiose. If you already mentor undergrads in your lab, explain how this project will train them in new techniques. If you have existing connections to a local K-12 program, describe how you’ll use them—don’t manufacture new partnerships from whole cloth.

Here’s the tell: “We will develop outreach materials” raises immediate skepticism. But “I teach a summer workshop at Lincoln High School’s science program—this research will provide three new hands-on modules on climate modeling” builds trust. One is a vague promise. The other is a concrete plan rooted in existing relationships.

Lesson 4: Budget Justification Actually Matters

I used to think budgets were purely administrative. Surely reviewers barely glanced at them—they cared about the science, not the accounting, right? Standard rates and percentages seemed perfectly sufficient.

Reviewers absolutely read budget justifications. We look for alignment between what you’re proposing to do and what you’re proposing to spend. Misalignment raises immediate red flags. And here’s something that surprised many junior faculty I’ve mentored: over-budgeting is just as problematic as under-budgeting.

Every major budget line should connect clearly to a specific aim in your proposal. Justify why you need that piece of equipment—what will it do that your existing infrastructure can’t? Personnel effort should match the work described. If you’re requesting 50% effort for a postdoc, reviewers should see that postdoc playing a central role in half your aims.

Red flags I’ve seen repeatedly: proposing ambitious international fieldwork with minimal travel budget or requesting full postdoc salary when the proposal’s narrative gives that postdoc almost nothing to do. These inconsistencies make reviewers wonder whether you’ve really thought through how the work will get done.

Lesson 5: How You Handle Weaknesses Reveals Everything

I once believed you should never acknowledge limitations. Defend every choice—project confidence at all costs. Any admission of weakness would be seized upon by reviewers looking for reasons to reject your proposal.

This might be the lesson I wish I’d learned earliest. Reviewers already see the weaknesses in your proposal. Pretending problems don’t exist destroys your credibility far more than the limitations themselves.

How you address limitations reveals your scientific maturity. Acknowledge real problems early and directly. Then explain your mitigation strategy: “If plan A fails, we will try plan B because…” Show you’ve thought through alternatives and have realistic contingency plans.

This lesson became even clearer when I started seeing resubmissions. The response letter matters as much as the revised proposal itself. A defensive tone—arguing with reviewers, insisting they misunderstood you—equals instant rejection. But a response that says “We appreciate the panel’s insights. We have substantially revised Section 2.3 to address concerns about statistical power. New preliminary data (Figure 3) demonstrates feasibility of the alternative approach” shows growth and responsiveness.

Panels respect PIs who demonstrate scientific judgment far more than those who claim perfection. We know perfect proposals don’t exist. We want to see that you can identify problems and solve them.

Lesson 6: The Human Element of Review

I believed grant review was a purely objective, data-driven process where careful reviewers gave equal attention to every proposal, systematically evaluating each against clear criteria.

Reviewers are human. They’re tired. They’re distracted. They have bad days. Panel dynamics matter—who speaks up first, who’s respected, who’s combative. Your proposal isn’t evaluated in isolation; it competes with the others in that review cycle, and comparison effects are real even if the program officers say it shouldn’t be.

Here’s the practical reality: reviewers read proposals at night, on weekends, while traveling. They’re squeezing this work into already overwhelming schedules. If they’re confused by page two, they may never fully engage with your brilliant idea on page eight. Your first page matters disproportionately.

Make your innovation immediately clear. Give reviewers ammunition to advocate for you in panel discussions—clear summary statements they can quote, compelling preliminary data they can point to. The discussant’s job is to convince other panelists to fund your work. Make their job easy.

This isn’t unfair. It’s simply reality. Design your proposal for the actual conditions of review, not the idealized version where everyone reads every word with perfect attention on a quiet Sunday morning with fresh coffee.

Lesson 7: Resubmissions Are About Demonstrating You Listened

I initially thought resubmissions were second chances to explain myself better. The reviewers had clearly misunderstood my brilliant idea. Now I’d show them what I really meant, with more precise explanations and stronger arguments.

Resubmissions are about showing scientific growth. They demonstrate whether you can receive criticism, integrate feedback, and improve your work. The reviewers weren’t wrong—or at least, whether they were wrong doesn’t matter. What matters is whether you can respond constructively to their concerns.

Start your response letter with genuine gratitude, not perfunctory politeness. Group your responses to criticisms thematically rather than addressing them line by line, which makes you look defensive. Show clearly what you changed and where reviewers can find those changes in the revised proposal. If you genuinely disagree with a criticism, do so respectfully and support your position with data, not rhetoric.

The successful resubmissions I’ve seen follow a pattern: acknowledge the feedback, explain the changes, demonstrate improvement with new evidence. The unsuccessful ones argue, defend, and explain why the reviewers didn’t understand the first time.

What These Lessons Reveal About Science Funding

These aren’t just tips for better grant writing. They reveal something more profound about how American science funding works. As I’ve written before, the current system prioritizes risk mitigation over bold ideas. It values clear communication and demonstrates competence over theoretical brilliance. It rewards incremental progress from established investigators more readily than moonshots from newcomers.

I’m not criticizing (this time)—it’s how the system is designed. When you’re allocating hundreds of millions in taxpayer dollars, trust and deliverability matter. Understanding this cultural logic helps you work within the system more effectively.

And it raises an interesting question I’m exploring in my new work on international science policy: Do other countries fund science differently because they assess risk differently? Do European or Asian funding systems embed different assumptions about what science should accomplish? That’s a topic for future posts.

These lessons came from mistakes, from failed proposals, from thousands of hours in review rooms watching good science get rejected for preventable reasons. I wish I’d understood them earlier in my career. I’m offering them now to help you avoid the same learning curve.

What hard-won lessons have you learned about grant writing? What advice would you give your younger self? Share in the comments.

As you prepare your 2026 submissions, remember there’s a human being on the other side of your proposal. Make their job easier. Help them advocate for your science. Give them reasons to say yes.

Why I’m Taking Science Policy Insider International

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A View from Abroad

Mid-competition week for a panel reviewing proposals on genes and cells: the fifteen-minute clock starts, and the five of us assigned to this proposal dive in. We consider factors such as whether the proposer is early in their career and how the COVID pandemic might have affected their laboratory’s productivity. We carefully assess their plan for mentoring trainees, including their previous track record and plans. The excellence of the proposer is evaluated, not by raw bibliometric measures such as H-index, but by substantive contributions to the field. And we take a very close look at the proposal itself—not only in terms of intellectual merit, but also to make sure that it is distinct from the investigator’s other supported science. Is this an NIH study section? Nope. Is this an NSF panel? Again, no. This is a peer review for another G7 nation, to be unnamed in this post.

What struck me wasn’t that this country did peer review differently than NSF or NIH. What struck me was how similar it was. Same careful attention to mentoring. Same suspicion of bibliometrics. Same concern about overlaps with existing funding. I could have been in any panel room I’d sat in over three decades in Washington. And that’s when it hit me: among the wealthy nations that fund science, we’re all running variations on the same basic system. We argue about details – overhead rates, review criteria, funding durations – but we share fundamental assumptions about how science should work.

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Or so I thought. Until I stepped outside the world of science funding and began looking at how other countries organize technical knowledge. My second book project examines how Boeing, Airbus, and Embraer design commercial aircraft – and that research has revealed something I’d missed in all my years in government and academia.

Civic Epistemologies

The scholar Sheila Jasanoff has a concept called ‘civic epistemologies’ – the idea that different societies have fundamentally different ways of producing and validating knowledge. It’s not about organizational charts or funding mechanisms. It’s deeper than that. It’s about cultural assumptions: What questions are worth asking? What counts as evidence? Who gets to decide? How do we measure success?

When Americans design an airplane, we assume that technical decisions should be made by engineers based on data, with regulators checking compliance after the fact. Europeans embed social and labor concerns directly into the design process – workers’ councils have a say in production methods, and safety regulators are involved earlier. Brazilians organize around different assumptions entirely, shaped by their position as a developing economy entering a market dominated by established players.

Same engineering principles. Same physics. The same goal of building a safe, efficient aircraft. But fundamentally different answers to the question: Who should decide how this gets done?

I saw the same pattern as a working neuroscientist. American neuroscience tends to bet on fundamental discovery—map the circuits, understand the mechanisms, and applications would follow. Recording sea slug neurons during my training embodied this approach: study simpler systems, find conserved principles, apply them to humans. Europeans start closer to the clinic, organizing major research programs around disease categories and patient needs. Japanese neuroscience builds unusually tight links between academic labs and industry—electronics and engineering companies actively embedded in research networks, with clear paths toward commercialization: same neurons, same biology—different assumptions about how knowledge should flow from laboratory to society.

My new book project

So, where is this taking me? The short answer is I’m working on a new book about how American, European, and Brazilian cultures (think Boeing, Airbus, and Embraer) shape commercial aviation technology. Why planes? In my lifetime, I experienced firsthand the jet revolution: I started on the Comet, went on to the Pan Am 707s, and these days still enjoy the grandeur of the big twin aisle giants that connect us across oceans.

In the new book, I’m interested in comparing technical cultures through the lens of those jets (as technical artifacts). But beyond my lifetime fascination with aviation, the same questions apply to science policy itself: why do different countries organize technological knowledge differently? What can we learn from how other G7 nations fund science? And what cultural assumptions shape what gets built (airplanes OR research programs)?

Science Policy Insider Expands Its Scope

This brings me back to Science Policy Insider and where we’re headed. We are broadening our remit. In the future, we’ll expand to include a comparative analysis of research funding systems—both public agencies and private industry—drawing on insights from my aviation research. We’ll examine how different countries handle current challenges: AI governance, climate research, and research security.

On the practical side, we’ll provide insights for American researchers who work internationally or plan to—from navigating different grant systems to understanding why collaborations succeed or fail across cultural boundaries. And above all, we’ll consider what viewing American science policy from the outside reveals about our own system.

We’ll maintain our bi-weekly publishing schedule.

Science Policy Insider started with my promise to explain how American science policy really works from someone who was inside the system. Now we’re also going to explore what it looks like from the outside and what that perspective reveals about our own system.

I continue to invite readers’ questions, now not only about how things work in our own American discovery machine, but also about international science policy.

Grades posted: another semester in the books

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Fall semester 2025 is now complete. Both my undergraduates and my grad students performed very well. When we begin this all again in Spring, I’ll be teaching my favorite class on Space governance, using Kim Stanley Robinson’s Mars Trilogy as our text. And we’ll be teaching our crisis management class again — this time to a new cohort of Schar School master’s students.

But for now, it’s time for the winter break. I’m 2/3 of the way through my reread of Moby Dick. And James Joyce’s Ulysses is on deck. I’ve got a ton of grant proposals headed my way to review for the Canadian NSERC to relieve the excess literary fiction.

How Will You Know You’ve Succeeded? A BRAIN story

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August 2008: A summer day in Mountain View California. The previous year, In 2007, The Krasnow Institute for Advanced Study, which I was leading at George Mason University, had developed a proposal to invest tons of money in figuring out how mind emerges from brains and now I had to make the case that it deserved to be a centerpiece of a new administration’s science agenda. Three billion dollars is not a small ask, especially in the context of the 2008 financial crisis that was accelerating.

Before this moment, the project had evolved organically: a kickoff meeting at the Krasnow Institute near D.C., a joint manifesto published in Science Magazine, and then follow-on events in Des Moines, Berlin and Singapore to emphasize the broader aspects of such a large neuroscience collaboration. There even had been a radio interview with Oprah.

When I flew out to Google’s Mountain View headquarters in August 2008 for the SciFoo conference, I didn’t expect to be defending the future of neuroscience over lunch. But the individual who was running the science transition for the Obama Presidential Campaign, had summoned me for what he described as a “simple” conversation: defend our idea for investing $3 billion over the next decade in neuroscience with the audacious goal of explaining how “mind” emerges from “brains.” It was not the kind of meeting I was ready for.

I was nervous. As an institute director, I’d pitched for million-dollar checks. This was a whole new scale of fundraising for me. And though, California was my native state, I’d never gone beyond being a student body president out there. Google’s headquarters in summer of 2008 was an altar to Silicon Valley power.

SciFoo itself was still in its infancy then – the whole “unconference” concept felt radical and exciting, a fitting backdrop for pitching transformational science. But the Obama campaign wasn’t there for the unconventional meeting format. Google was a convenient meeting spot. And they wanted conventional answers.

I thought I made a compelling case: this investment could improve the lives of millions of patients with brain diseases. Neuroscience was on the verge of delivering cures. (I was wrong about that, but I believed it at the time.) The tools were ready. The knowledge was accumulating. We just needed the resources to put it all together.

Then I was asked the question that killed my pitch: “How will we know we have succeeded? What’s the equivalent of Kennedy’s moon landing – a clear milestone that tells us we’ve achieved what we set out to do?” You could see those astronauts come down the ladder of the lunar module. You could see that American flag on the moon. No such prospects with a large neuroscience initiative.

I had no answer.

I fumbled through some vague statements about understanding neural circuits and developing new therapies, but even as the words left my mouth, I knew they were inadequate. The moon landing worked as a political and scientific goal because it was binary: either we put a man on the moon or we didn’t. Either the flag was planted or it wasn’t.

But “explaining how mind emerges from brains”? When would we know we’d done that? What would success even look like?

The lunch ended politely. I flew back to DC convinced it had been an utter failure.

But that wasn’t the end of it. Five years later, at the beginning of Obama’s second presidential term, we began to hear news of a large initiative driven by the White House called the Brain Activity Map or BAM for short. The idea was to comprehensively map the functional activity of brains at high spatial and temporal resolution beyond that available at the time. It was like my original pitch both in scale (dollars) and in the notion that it was important to understand how mind emerges from brain function. The goal for the new BAM project was to be able to map between the activity and the brain’s emergent “mind”-like behavior, both in the healthy and pathological cases. But the BAM project trial balloon, even coming from the White House, was not an immediate slam dunk.

There was immediate push-back from large segments of the neuroscience community that felt excluded from BAM, but with a quick top-down recalibration from the White House Office of Science and Technology Policy and a whole of government approach that included multiple science agencies, BRAIN (Brain Research through Advancing Innovative Neurotechnologies) was born in April of 2013.

A year later, in April of 2014, I was approached to head Biological Sciences at the US National Science Foundation. When I took the job that October, I was leading a directorate with a budget of $750 million annually that supported research across the full spectrum of the life sciences – from molecular biology to ecosystems. I would also serve as NSF’s co-lead for the Obama Administration’s BRAIN Initiative—an acknowledgement of the failed pitch in Mountain View, I guess.

October 2014: sworn in and meeting with my senior management team–now here I was, a little more than a year into BRAIN. I had gotten what I’d asked for in Mountain View. Sort of. We had the funding, we had the talent, we had review panels evaluating hundreds of proposals. But I kept thinking about the question—the one I couldn’t answer then and still struggled with now. We had built this entire apparatus for funding transformational research, yet we were asking reviewers to apply the same criteria that would have rejected Einstein’s miracle year. How do you evaluate research when you can’t articulate clear success metrics? How do you fund work that challenges fundamental assumptions when your review criteria reward preliminary data and well-defined hypotheses?

Several months later, testifying before Congress about the BRAIN project, I remember fumbling again at the direct question of when we would deliver cures for dreaded brain diseases like ALS and Schizophrenia. I punted: that was an NIH problem (even though the original pitch had been about delivering revolutionary treatments. At NSF, we were about understanding the healthy brain. In fact, how could you ever understand brain disease without a deep comprehension of the non-pathological condition?

It was a reasonable bureaucratic answer. NIH does disease; NSF does basic science. Clean jurisdictional boundaries. But sitting there in that hearing room, I realized I was falling into the same trap that had seemingly doomed our pitch in 2008: on being asked for the delivery date of a clear criterion for success, I was waffling. Only this time, I was the agent for the funder: the American taxpayer.

The truth was uncomfortable. We had launched an initiative explicitly designed to support transformational research – research that would “show us how individual brain cells and complex neural circuits interact” in ways we couldn’t yet imagine. But when it came time to evaluate proposals, we fell back on the same criteria that favored incrementalism: preliminary data, clear hypotheses, established track records, well-defined deliverables. We were asking Einstein for preliminary data on special relativity.

And we weren’t unique. This was the system. This was how peer review worked across federal science funding. We had built an elaborate apparatus designed to be fair, objective, and accountable to Congress and taxpayers. What we had built was a machine that systematically filtered out the kind of work that might transform neuroscience.

All of this was years before the “neuroscience winter”—where massive scientific misconduct was unearthed in neurodegenerative disease research—which included Alzheimer’s. But the modus operandi of BRAIN foreshadowed it.

Starting in 2022, a series of investigations revealed that some of the most influential research on Alzheimer’s disease—work that had shaped the field for nearly two decades and guided billions in research funding—was built on fabricated data. Images had been manipulated. Results had been doctored. And this work had sailed through peer review at top journals, had been cited thousands of times, and had successfully competed for grant funding year after year. The amyloid hypothesis, which this fraudulent research had bolstered, had become scientific orthodoxy not because the evidence was overwhelming, but because it fit neatly into the kind of clear, well-defined research program that review panels knew how to evaluate.

Here was the other side of the Einstein problem that I’ve mentioned in previous posts. The same system that would have rejected Einstein’s 1905 papers for lack of preliminary data and institutional support had enthusiastically funded research that looked rigorous but was fabricated. Because the fraudulent work had all the elements that peer review rewards: clear hypotheses, preliminary data, incremental progress building on established findings, well-defined success metrics. It looked like good science. It checked all the boxes.

Meanwhile, genuinely transformational work—the kind that challenges fundamental assumptions, that crosses disciplinary boundaries, that can’t provide preliminary data because the questions are too new—struggles to get funded. Not because reviewers are incompetent or malicious, but because we’ve built a system that is literally optimized to make these mistakes. We’ve created an apparatus that rewards the appearance of rigor over actual discovery, that favors consensus over challenge, that funds incrementalism and filters out transformation.

So, what’s the real function of peer review? It’s supposed to be about identifying transformative research, but I don’t think that the real purpose. To my mind, the real purpose of peer review panels at NSF, the study sections at NIH, is to make inherently flawed funding decisions defensible—both to Congress and the American taxpayer. The criteria, intellectual merit, broader impacts at NSF, make awarding grant dollars auditable and fair seeming, not because they identify breakthrough work.

But honestly, there’s a real dilemma here: if you gave out NSF’s annual budget based on a program officer’s feeling that “this seems promising”, you’d face legitimate questions about cronyism, waste and arbitrary decision-making. The current system’s flaws aren’t bad policy accidents; they are the price we pay for other values we also care about.

So, did the BRAIN Initiative deliver on that pitch I made in Mountain View in 2008? Did we figure out how ‘mind’ emerges from ‘brains’? In retrospect, I remain super impressed by NSF’s  NeuroNex program: we got impressive technology – better ways to record from more neurons, new imaging techniques, sophisticated tools. We trained a generation of neuroscientists. But that foundational question – the one that made the political case, the one that justified the investment – we’re not meaningfully closer to answering it. We made incremental progress on questions we already knew how to ask. Which is exactly what peer review is designed to deliver. Oh, and one other thing that was produced: NIH’s parent agency, the Department of Health and Human Services,  got a trademark issued on the name of the initiative itself, BRAIN.

I spent four years as NSF’s co-lead on BRAIN trying to make transformational neuroscience happen within this system. I believed in it. I still believe in federal science funding. But I’ve stopped pretending the tension doesn’t exist. The very structure that makes BRAIN funding defensible to Congress made the transformational science we promised nearly impossible to deliver.

That failed pitch at Google’s headquarters in 2008. Turns out that the question was spot on we just never answered it.

Why Transformational Science Can’t Get Funded: The Einstein Problem

Proposal declined. Insufficient institutional support. No preliminary data. Applicant lacks relevant expertise—they work in a patent office, not a research laboratory. The proposed research is too speculative and challenges well-established physical laws without adequate justification. The principal investigator is 26 years old and has no prior experience in physics.

This would have been the fate of Albert Einstein in 1905, had the NSF existed as it does today. Even with grant calls requesting ‘transformative ideas,’ an Einstein proposal would have been rejected outright. And yet, that year 1905 has been called Einstein’s miracle year. Yes, he was a patent clerk working in Bern, Switzerland, without a university affiliation. He had neither access to a laboratory nor equipment. He worked in isolation on evenings and weekends and was unknown in the physics community. Yet, despite those disadvantages, he produced four revolutionary papers on the Photoelectric Effect, Brownian motion, Special Relativity, and the famous E=mc2 energy-mass equivalence.

Taken as a whole, the work was purely theoretical. There were no preliminary data. The papers challenged fundamental assumptions of the field and, as such, were highly speculative and definitively high-risk. There were no broader impacts because there were no immediate practical applications. And the work was inherently multidisciplinary, bridging mechanics, optics, and thermodynamics. Yet, the work was transformative. By modern grant standards, Einstein’s work failed every criterion.

The Modern Grant Application – A Thought Experiment

Let’s imagine Einstein’s 1905 work packaged as a current NSF proposal. What would it look like, and how would it fare in peer review?

Einstein’s Hypothetical NSF Proposal

Project Title: Reconceptualizing the Fundamental Nature of Space, Time, and the Propagation of Light

Principal Investigator: Albert Einstein, Technical Expert Third Class, Swiss Federal Patent Office

Institution: None (individual applicant)

Requested Duration: 3 years

Budget: $150,000 (minimal – just salary support and travel to one conference)

Project Summary

This proposal challenges the fundamental assumptions underlying Newtonian mechanics and Maxwell’s electromagnetic theory. I propose that space and time are not absolute but relative, dependent on the observer’s state of motion. This requires abandoning the concept of the luminiferous ether and reconceptualizing the relationship between matter and energy. The work will be entirely theoretical, relying on thought experiments and mathematical derivation to establish a new framework for understanding physical reality.

How NSF Review Panels Would Evaluate This

Intellectual Merit: Poor

Criterion: Does the proposed activity advance knowledge and understanding?

Panel Assessment: The proposal makes extraordinary claims without adequate preliminary data. The applicant asserts that Newtonian mechanics—the foundation of physics for over 200 years—requires fundamental revision yet provides no experimental evidence supporting this radical departure.

Specific Concerns:

Lack of Preliminary Results: The proposal contains no preliminary data demonstrating the feasibility of the approach. There are no prior publications by the applicant in peer-reviewed physics journals. The applicant references his own unpublished manuscripts, which cannot be evaluated.

Methodology Insufficient: The proposed “thought experiments” do not constitute rigorous scientific methodology. How will hypotheses be tested? What experimental validation is planned? The proposal describes mathematical derivations but provides no pathway to empirical verification. Without experimental confirmation, these remain untestable speculations.

Contradicts Established Science: The proposal challenges Newton’s laws of motion and the existence of the luminiferous ether—concepts supported by centuries of successful physics. While scientific progress requires questioning assumptions, such fundamental challenges require extraordinary evidence. The applicant provides none.

Lack of Expertise: The PI works at a patent office and has no formal research position. He has no advisor supporting this work, no collaborators at research institutions, and no track record in theoretical physics. His biosketch lists a doctorate from the University of Zurich but no subsequent research appointments or publications in relevant areas.

Representative Reviewer Comments:

Reviewer 1: “While the mathematical treatment shows some sophistication, the fundamental premise—that simultaneity is relative—contradicts basic physical intuition and has no experimental support. The proposal reads more like philosophy than physics.”

Reviewer 2: “The applicant’s treatment of the photoelectric effect proposes that light behaves as discrete particles, directly contradicting Maxwell’s well-established wave theory. This is not innovation; it’s contradiction without justification.”

Reviewer 3: “I appreciate the applicant’s ambition, but this proposal is not ready for funding. I recommend the PI establish himself at a research institution, publish preliminary findings, and gather experimental evidence before requesting support for such speculative work. Perhaps a collaboration with experimentalists at a major university would strengthen future submissions.”

Broader Impacts: Very Poor

Criterion: Does the proposed activity benefit society and achieve specific societal outcomes?

Panel Assessment: The proposal fails to articulate any concrete broader impacts. The work is purely theoretical with no clear pathway to societal benefit.

Specific Concerns:

No Clear Applications: The proposal does not explain how reconceptualizing space and time would benefit society. What problems would this solve? What technologies would it enable? The PI suggests the work is “fundamental” but provides no examples of potential applications.

No Educational Component: There is no plan for training students or postdocs. The PI works alone at a patent office, with no access to students and no institutional infrastructure for education and training.

No Outreach Plan: The proposal includes no activities to communicate findings to the public or policymakers. There is no plan for broader dissemination beyond potential publication in physics journals.

Questionable Impact Timeline: Even if the proposed theories are correct, the proposal provides no timeline for practical applications. How long until these ideas translate into societal benefit? The proposal is silent on this critical question.

Representative Reviewer Comments:

Reviewer 1: “The broader impacts section is essentially non-existent. The PI states that ‘fundamental understanding of nature has intrinsic value,’ but this does not meet NSF’s requirement for concrete societal outcomes.”

Reviewer 2: “I cannot envision how this work, even if successful, would lead to practical applications within a reasonable timeframe. The proposal needs to articulate a clear pathway from theory to impact.”

Reviewer 3: “NSF has limited resources and must prioritize research with demonstrable benefits to society. This proposal does not make that case.”

Panel Summary and Recommendation

Intellectual Merit Rating: Poor
Broader Impacts Rating: Very Poor

Overall Assessment: While the panel appreciates the PI’s creativity and mathematical ability, the proposal is highly speculative, lacks preliminary data, contradicts established physical laws without sufficient justification, and fails to articulate broader impacts. The PI’s lack of institutional affiliation and research track record raises concerns about feasibility.

The panel notes that the PI appears talented and encourages resubmission after:

  1. Establishing an independent position at a research institution
  2. Publishing preliminary findings in peer-reviewed journals
  3. Developing collaborations with experimental physicists
  4. Articulating a clearer pathway to practical applications
  5. Demonstrating broader impacts through education and outreach

Recommendation: Decline

Panel Consensus: Not competitive for funding in the current cycle. The proposal would need substantial revision and preliminary results before it could be considered favorably.

The Summary Statement Einstein Would Receive

Dear Dr. Einstein,

Thank you for your submission to the National Science Foundation. Unfortunately, your proposal, “Reconceptualizing the Fundamental Nature of Space, Time, and the Propagation of Light,” was not recommended for funding.

The panel recognized your ambition and mathematical capabilities but identified several concerns that prevented a favorable recommendation:

– Lack of preliminary data supporting the feasibility of your approach – Insufficient experimental validation of your theoretical claims
– Absence of institutional support and research infrastructure – Inadequate articulation of broader impacts and societal benefits

We encourage you to address these concerns and consider resubmission in a future cycle. You may wish to establish collaborations with experimentalists and develop a clearer pathway from theory to application.

We appreciate your interest in NSF funding and wish you success in your future endeavors.

Sincerely,
NSF Program Officer

And that would be it. Einstein’s miracle year—four papers that transformed physics and laid the groundwork for quantum mechanics, nuclear energy, GPS satellites, and our modern understanding of the cosmos—would have died in peer review, never funded, never attempted.

The system would have protected us from wasting taxpayer dollars on such speculation. It would have worked exactly as designed.

The Preliminary Data Paradox

The contemporary scientific grant review process implicitly expects foundational work in transformative science to present preliminary data, despite knowing that truly groundbreaking ideas often do not originate from such tangible evidence but instead evolves through thought experiments and mathematical derivations, as Einstein did. This unrealistic expectation stifles innovation at its core – the process essentially forces researchers like Einstein to abandon pure theoretical exploration and confine them to a narrow experimental framework, where they cannot freely challenge existing paradigms, even when their work holds no immediate empirical validation yet promises to revolutionize our understanding fundamentally.

The Risk-Aversion Problem

Often, in grant reviews, I see a very junior reviewer criticize work as being too risky—dooming the proposal to failure—while simultaneously sensing their admiration for the promise and transformative nature of the work. The conservative nature and risk-averse mentality of modern grant review panels are deeply rooted in the scientific community’s culture that values incremental advances over speculative leaps – a bias born from career motivations wherein funding decisions can make or break one’s professional trajectory. Reviewers often exhibit reluctance to invest support into proposals like Einstein’s, as they pose potential controversy and may not align with personal research interests due to the associated risks of failure – a reflection of how science has traditionally evolved through evolutionary rather than revolutionary processes within academic institutions.

The Credentials Catch-22

To secure funding in today’s scientific landscape, one often needs institutional affiliation and an impressive publication record that reflects strong research credentials – a catch-22 scenario wherein groundbreaking innovators with no formal backing or prior experience find it challenging to gain the trust of reviewers. This requirement discriminates against fresh perspectives from individuals such as Einstein, who was working outside established institutions and did not have access to mentorship, which is typically deemed necessary for academic recognition – a stark contrast in how transformative outsider thinkers with unconventional backgrounds historically nurtured science.

The Short-Term Timeline Problem

Einstein developed special relativity over years with no milestones, no quarterly reports, no renewals. How would he answer, ‘What will you accomplish in Year 2?” The funding cycle durations set forth by major grant agencies, such as NSF’s typical three to five years for regular grants and the NIH’s maximum of five years, do not accommodate the long periods necessary for fully developing foundational theories that require time-intensive evolution. Such timelines impose an unfair constraint on researchers like Einstein, whose transformative ideas did not evolve within strict milestones but unfolded in an unconstrained fashion – showcasing the incompatibility of this model with truly revolutionary scientific discoveries where a linear progression is unrealistic and even counterproductive.

The Impact Statement Trap

Requirements for demonstrating immediate “broader impacts” or societal benefits pose significant obstacles to transformative research proposals that often envision far-reaching implications beyond their direct applications – an aspect Einstein’s work exemplifies best with its foundational role in advancing physics. The trap lies when reviewers, fearing potential misuse of speculative science or unable to perceive future benefits due to cognitive biases, force research proposals into a mold where immediate practical impact takes precedence over visionary scientific contributions, further marginalizing transformative studies that could potentially unlock new dimensions in various fields.

The Interdisciplinary Gap

The inherent disciplinarity of current grant funding schemes disconnects them from the interdisciplinary essence required for revolutionary research proposals like Einstein’s – a reality where transformative work frequently transcends conventional academic boundaries by merging concepts across multiple fields. This approach often results in an exclusion not only based on institutional affiliation but also because of its challenge to compartmentalized funding models that struggle with the non-linear, cross-disciplinary nature integral to truly transformative science – a significant obstacle for proposals inherently interdisciplinary yet unable to fit neatly within program structures or expertise.

The hypothetical funding scenarios for transformational science, as presented through the lens of Albert Einstein’s groundbreaking work, illustrate the inherent challenges faced by revolutionary ideas. To further highlight this problem, let’s take a look at other seminal discoveries that may have been overlooked or deemed unworthy of support under current grant review criteria:

Copernicus’ Heliocentric Model: In a contemporary setting, Copernicus’ heliocentric model might face skepticism due to its challenge to the widely accepted geocentric view of the universe. Lacking preliminary data and facing resistance from established religious beliefs, his proposal would likely be rejected under modern grant review criteria, despite its ultimate validation through observation and mathematical proof.

Gregor Mendel’s Pea Plant Experiments: The foundation of modern genetics was laid by Mendel’s pea plant experiments, yet his work remained largely unnoticed for decades after its initial publication. A grant reviewer in 1863 would likely have dismissed Mendel’s findings as too speculative and without immediate practical applications, thereby overlooking the fundamental insights he provided about heredity and genetic inheritance.

mRNA Vaccines: Katalin Karikó spent decades struggling to fund mRNA therapeutic research. Too risky. Too speculative. No clear applications. Penn demoted her. NIH rejected her grants. Reviewers wanted proof that mRNA could work as a therapeutic platform, but without funding, she couldn’t generate that proof. Then COVID-19 hit, and mRNA vaccines saved millions of lives. The technology that couldn’t get funded became one of the most important medical breakthroughs of the century.

Why does all of this matter now? First, the evidence is mounting that American science is at an inflection point. The rate of truly disruptive discoveries—those that reshape fields rather than incrementally advance them—has been declining for decades, even as scientific output has grown. Both NSF and NIH leadership recognize this troubling trend.

This innovation crisis manifests in the problems we cannot solve. Cancer and Alzheimer’s have resisted decades of intensive research. AI alignment and safety remain fundamentally unsolved as we deploy increasingly powerful systems. We haven’t returned to the moon in over 50 years. In my own field of neuroscience, incremental progress has failed to produce treatments for the diseases that devastate millions of families.

These failures point to a deeper problem: we’ve optimized our funding system for incremental advances, not transformational breakthroughs. Making matters worse, we’re losing ground internationally. China’s funding models allow longer timelines and embrace higher risk. European ERC grants support more adventurous research. Many of our best researchers now weigh opportunities overseas or in industry, where they can pursue riskier ideas with greater freedom.

What Needs to Change

Fixing this requires fundamental changes at multiple levels—from how we structure programs to how we evaluate proposals to how we support unconventional researchers.

Create separate funding streams for high-risk research. NSF and NIH need more programs that emulate DARPA’s high-risk, high-reward model. These programs should be insulated from traditional grant review: no preliminary data required, longer timelines (10+ years), and peer review conducted by scientists who have themselves taken major risks and succeeded. I propose that 10 percent of each agency’s budget be set aside for “Einstein Grants”—awards that take the view opposite the status quo. Judge proposals on originality and potential impact, not feasibility and preliminary data. Accept that most will fail, but the few that succeed will be transformational.

Protect exploratory research within traditional programs. Even standard grant programs should allow pivots when researchers discover unexpected directions. We should fund people with track records of insight, not just projects with detailed timelines. Judge proposals on the quality of thinking, not the completeness of deliverables.

Reform peer review processes. The current system needs three critical changes. First, separate review tracks for incremental versus transformational proposals—they require fundamentally different evaluation criteria. Second, don’t let a single negative review kill bold ideas; if three reviewers are enthusiastic and one is skeptical, fund it. Third, value originality over feasibility. The most transformational ideas often sound impossible until someone proves otherwise.

Support alternative career paths. We should fund more researchers outside traditional academic institutions and recognize that the best science doesn’t always emerge from R1 universities. Explicitly value interdisciplinary training and create flexible career paths that don’t punish researchers who take time to develop unconventional ideas. Track where our most creative researchers go when they leave academia—if we’re consistently losing them to industry or foreign institutions, that’s a failure signal we must heed.

Acknowledge the challenge ahead. These reforms require sustained political will across multiple administrations and consistent support from Congress. They demand patience—accepting that transformational breakthroughs can’t be scheduled or guaranteed. But the alternative is clear: we continue optimizing for incremental progress while the fundamental problems remain unsolved and our international competitors embrace the risk we’ve abandoned.

The choice before us is stark. We can optimize the current system for productivity—incremental papers, measurable progress—or we can create space for transformative discovery. We cannot have both with the same funding mechanisms.

The cost of inaction is clear: we will miss the next Einstein, fall further behind in fundamental discovery, watch science become a bureaucratic exercise, and lose what made American science into a powerhouse of discovery.

This requires action at every level. Scientists must advocate for reform and be willing to champion risky proposals. Program officers must have the courage to fund work that reviewers call too speculative. Policymakers must create new funding models and resist the temptation to demand near-term results. The public must understand that breakthrough science looks different from incremental progress—it’s messy, unpredictable, and often wrong before it’s right.

In 1905, Einstein changed our understanding of the universe while working in a patent office with no grant funding. Today, our funding system would never have let him try. We need to fix that.