Why Is Great Innovation Impossible to Plan? | 5Y View

Today's article comes from the book Why Greatness Cannot Be Planned. Both authors, Kenneth Stanley and Joel Lehman, currently serve as research scientists at OpenAI. They have spent years working at the frontier of artificial intelligence, and this book emerged as an unexpected spark from their scientific research — an exploration of how innovation actually happens.

The authors argue that consensus is often the enemy of innovation, and that blind faith in goal-based evaluation leads to mediocrity and conformity. There are many novel things waiting to be discovered, but finding them requires sustained intellectual investment and an open mind.

It is at the boundary between the known and unknown, in the non-consensus "wilderness," that humanity's greatest minds continuously explore — this is the path to innovation. We hope this article offers you some inspiration :)

This excerpt is adapted from Chapter 8 of Why Greatness Cannot Be Planned, with some abridgments.

Authors: Kenneth Stanley, Joel Lehman

Scientists seeking new exploration and discovery must first secure funding for their experiments. It turns out that decisions about which scientific experiments to fund are often heavily influenced by goal-oriented thinking.

This is a critical issue because mistaken investment decisions can impede scientific progress and carry potential societal consequences. In the long run, we can easily see where the deceptive influence of goals manifests in science.

Intuitively, it seems wiser to invest in scientific projects whose researchers list clear objectives in their proposals and explicitly state what grand discoveries will emerge upon completion. But the lesson from Picbreeder is that the most interesting discoveries are often impossible to predict in advance, giving us reason to believe that non-goal (divergent) thinking may also reveal fundamental problems in how scientific projects are currently funded.

Advancing science makes for an interesting case study. Unlike education, science is an indispensable domain for driving new exploration and discovery, and individual failures carry relatively low risk. Overall, scientific exploration should be particularly well-suited to non-goal-oriented exploration. Yet we still see that even when occasional failure is acceptable, scientific activity frequently remains constrained by the deception of goals.

Consensus Is Often the Biggest Obstacle to Innovation

In many countries, including the United States, most research projects are funded through grants from government funding agencies. This support is crucial for advancing basic science because it backs research that lacks commercial viability. Of course, much funded science fails, because breakthrough ideas often carry extremely high risk of failure. So while some funded projects eventually succeed, many more will fail. This means that research funding agencies like the National Science Foundation (NSF) and the European Science Foundation (ESF) must take certain risks in their investment decisions if they hope to enable the most innovative ideas. It is therefore interesting to examine how these agencies make funding decisions, because here too we may face the deception and constraints of goals.

The general process for applying for research funding goes like this: scientists submit proposals to funding agencies, articulating their research ideas; these proposals are then sent to review panels composed of expert peer reviewers, typically senior scientists in the proposal's field; the reviewers assign ratings ranging from poor to excellent. Generally, proposals with the highest average ratings are most likely to receive funding.

At first glance, this seems like a perfectly reasonable screening process. Ideally, the best ideas in a given field should be able to convince a panel of professional scientists and earn top ratings. However, beneath this surface-level common sense lurks trouble, because the primary function of this review system is to support consensus. In other words, the more reviewers agree on a proposal's excellence, the more likely the agency is to fund it. The problem is that consensus is often the biggest obstacle to the stepping stones of success.

The issue here is that when people with opposing or different preferences are forced to vote, the winner often represents no one's actual preferences or ideals. Seeking consensus prevents people from pursuing interesting stepping stones, because different people may disagree on what constitutes the most interesting stepping stone. Resolving disagreements in taste among different groups tends to produce compromises between opposing stepping stones, much like mixing stark black and white together only yields a dull gray.

This compromised product ultimately dilutes the color of both original visions. For scientists writing proposals, the best way to win funding is to craft the perfect compromise — the softest gray that satisfies everyone's eye but is unlikely to deliver high novelty or interest. Thus, when people seek consensus in exploration, the entire system doesn't let each individual discover their own chain of stepping stones; instead, it compresses diverse opinions into a bland, safe average.

Perhaps sometimes it would make more sense to support maximum divergence rather than agreement. Opposing consensus may be more interesting than the flatness of "reaching agreement." After all, attracting unanimous votes is merely a sign of "following the herd, marching in lockstep." If you chase trendy research and parrot the majority, you may gain broad recognition and support; conversely, a truly interesting idea may spark controversy. At the boundary between what we currently know and don't know, there remain questions with uncertain answers. This is why in the unknown territories of science, expert opinions should remain divergent and dispersed. It is in this "wilderness" boundary zone between the known and unknown that we should let humanity's greatest minds explore, rather than indulging in the comfort zone of maximum consensus.

Consider: which project is likely to be more revolutionary — one with "mixed" reviews, or one with "universal acclaim"? Experts who disagree with each other may have greater capacity to drive great achievements than those who always agree.

Of course, this doesn't mean proposals with unanimous negative reviews should be funded. If all experts think an idea is terrible, all giving "poor" ratings, there's no evidence it's worth pursuing. But when experts have fundamental disagreements with each other, something interesting happens.

Darwin's theory of evolution was initially rejected by many experts — and that was actually a good sign! As American historian of science Thomas Kuhn's concept of paradigm shift suggests, cracks begin to appear in existing scientific frameworks. In these moments, discordant opinions are the prelude to revolutionary innovation. For all these reasons, some of our resources should be used to reward divergence rather than consensus.

This point also connects to goals, because rewarding consensus is grounded in goal-oriented thinking. From a goal-oriented perspective, the more experts agree that a particular path is worth taking, the more people should choose that path. A unanimously endorsed path represents a goal-based choice because everyone has agreed on its destination. And the number of experts offering unanimous opinion provides a measure of the best destination — this is goal-based evidence.

If your goal is to seek an idea that tends toward universal agreement, then consensus is certainly a praiseworthy ally. This is why in goal-driven search, the emphasis is always on the final destination rather than on the interestingness and novelty of the current stepping stone. This makes goal-based search incapable of being a "treasure hunter." Non-goal search discourages everyone from ending up on the same path or reaching the same destination — only under these conditions can interesting ideas attract resources and funding.

At this point, it's worth recalling the difference in search behavior between following interestingness and following objective performance. Science is one of humanity's greatest explorations, and reaching consensus before deciding on next steps amounts to strangling creative endeavor in the scientific domain. Of course, we're not suggesting that only controversial scientific proposals should be funded, but some portion of society's resources should indeed support interesting exploration. Scientific exploration similarly requires embracing the mindset of "treasure hunters" and "stepping stone collectors."

Of course, reaching consensus makes sense for certain types of decisions, but not for creative exploration. Our argument is that "disunity" — both between research groups and within the scientific exploration enterprise as a whole — can sometimes drive progress.

Not Knowing Where the Road Leads Is What Drives Human Innovation

Beyond pushing people toward consensus, goal-based thinking may influence research investment decisions in other ways. For example, if you're a believer in objectives, you might assume that the framework of scientific progress is predictable. In other words, according to the goal-oriented "where there's a will, there's a way" mentality, the stepping stones to major discoveries should line up in an orderly, predictable fashion.

Under this mindset, the key innovation for curing cancer would seemingly be an improvement or refinement of existing cancer treatments, or at least come from research directly related to cancer. Yet in this book, we have seen again and again that stepping stones to exceptional outcomes are unpredictable. So if we want to cure cancer, focusing solely on cancer may not get us to that grand goal. But even when research fails to achieve its original objective, its byproducts may yield unexpected breakthroughs in seemingly unrelated fields.

In fact, governments have already invested massive research funding in numerous targeted projects aimed at solving specific scientific problems. For example, Japan's Ministry of International Trade and Industry launched a large-scale ten-year research project in 1982, the "Fifth Generation Computer Systems Project," aimed at pushing Japanese computer technology to world leadership.

Although the Japanese government invested heavily in directed R&D, the project is widely considered to have failed to achieve its goal — developing products with commercial potential — though it did cultivate a new generation of promising Japanese computer researchers. Similarly, the "War on Cancer" launched by U.S. President Richard Nixon in 1971 (aimed at eliminating cancer as a high-mortality disease) has yet to succeed, despite targeted research into more effective cancer treatments and deeper understanding of tumor biology. In fact, seemingly unrelated scientific projects like the Human Genome Project hold more promise for discovering better cancer treatments.

Of course, sometimes ambitious scientific exploration programs do succeed. The U.S.-Soviet moon race of the 1960s, initiated by President Kennedy, who declared in his congressional address: "I believe that this nation should commit itself to achieving the goal, before this decade is out, of landing a man on the moon and returning him safely to the earth." But this uncertain declaration was achievable because it happened to sit right at the edge of technological possibility (that is, this grand goal was only one step away from realization at that time).

However, the potentially misleading conclusions about the power of goals drawn from these success stories often fuel naive goal optimism — the belief that with sufficient resources, any goal can be firmly established and certainly achieved at any point in history. For example, a former president of the American Cancer Society once said: "We are so close to curing cancer. We lack only the will, the funding, and the comprehensive planning that carried a man to the moon."

Finally, even in these grand scientific endeavors, the technologies that ultimately brought the most profound impact on human society were often unanticipated. The space race, for instance, gave us innovations like cochlear implants, memory foam mattresses, freeze-dried foods, and improved emergency blankets.

Although these grand-target scientific projects were clearly driven by goal-oriented thinking, they still offer some subtler lessons. A similar line of thinking holds that there is a predictable framework for how scientific projects impact the world.

That is, we might continuously invest to optimize those research projects that currently seem most likely to have impact, eventually producing some with breakthrough impact. The logic is that research projects with moderate impact will lead to more impactful ones, ultimately bringing disruptive change to the world through scientific exploration and discovery.

Following this logic, another manifestation of goal-driven thinking in research funding is judging whether a project merits investment based on the perceived importance of its expected impact. In fact, a major criterion used by funding agencies like the NSF in evaluating grant applications is the scope of the proposed research's impact. Thus, projects deemed to have smaller impact potential are less likely to receive funding.

Many people tend to ridicule research projects with seemingly whimsical goals — studies that obviously won't produce any important results — viewing them as pure wastes of money. This attitude reflects the same logic. Behind these examples lies a very seductive line of reasoning: that before a research project begins, we can classify it as important or unimportant based on whether the project and its outcomes will have broad societal impact.

By now, readers can probably see how arbitrary this thinking is — because many important discoveries are accidental or unexpected. Predicting the impact of research projects doesn't always work and can cause us to overlook the important role of serendipity. Moreover, even if we could pre-assess most research projects and reliably predict their impact, then fund only the most important ones, this would not be wise.

The key issue is that judging individual stepping stones by standards better suited to judging the entire system may be shortsighted. Ultimately, science as a whole aims to discover truths of depth and transformative power. But in this process, whether any particular research project is transformative may not matter at all. In fact, a research project being interesting and capable of generating even more interesting or unexpected experimental results may be more noteworthy than its own importance.

Picbreeder is one such example: as an overall system, it ultimately produced alien faces and car images that individual users could not have created alone. The novelty search case follows the same logic — as an exploration system, it might discover a maze-navigating robot, but only achieved this result when robots were not ranked by their maze-navigating ability.

Therefore, if we accept that stepping stones in scientific exploration are unpredictable, then "importance" may also be a deceptive standard in scientific exploration. Does a scientific result with certain importance necessarily bring us closer to transformative breakthroughs?

In other words, in scientific research, importance is just another broken objective compass. Because the stepping stones to the most important scientific discoveries may themselves be unimportant, and the stepping stones to the most disruptive technologies may show no transformative signs whatsoever.

Another approach to deciding whether to support major projects, or whether projects are worth investing in based on estimated impact, is to use the degree to which research projects serve particular interests as an investment criterion. This means governments may prefer to fund research agendas they consider important at the time, or projects that provide clear short-term benefits to the nation.

For example, according to the High Quality Research Act proposed by U.S. Representative Lamar Smith in 2013, before funding any research project, the NSF director must certify that the project "(1) is in the national interest of the United States by promoting the progress of science in order to advance the national health, prosperity, or welfare, and to secure the national defense; (2) is of the highest quality, is ground breaking, and answers questions or solves problems that are of the utmost importance to society at large; (3) is not duplicative of other research projects being funded by the Foundation or other federal science agencies."

The second provision assumes that judging whether research projects merit funding based on their importance is possible or desirable, while the first provision assumes that scientific research should proceed narrowly only in directions of direct national benefit, rather than conducting broader searches.

Although this bill had little chance of passing and being implemented in the United States, Canada has already enacted similar policies. In 2011, Canada's National Research Council (NRC) began redirecting research funding toward economic development at the expense of basic research.

Then-NRC president John McDougall explained that ultimately only 20% of the total budget would go to basic research areas like "curiosity and exploratory activities." By 2013, the NRC announced it was "opening its doors to research for business" and concentrating its funding on twelve "industry-themed entry points." The council claimed it was "reinventing itself to support Canadian industry... all these measures are aimed at one ultimate goal: providing high-quality jobs, increasing business R&D activity, achieving more commercialized results, and building a prosperous and more socially productive Canada."

This obvious shift meant investment priorities deviated from "basic research without direct practical value" toward narrowly aligning with national goals.

Of course, the idea that "simply pouring in large amounts of funding can reliably produce fundamental breakthroughs in specific important research areas" is very attractive, but narrowly framing priority research areas and grand goal-driven projects is actually undesirable. Because, regardless of how appealing its basic assumptions may be, this is simply not how the structure of scientific exploration operates.

Who can determine where the next great, commercializable technology will come from? So the crux is that goalless exploration may sound pessimistic about prospects, but it makes the world of science more interesting. There are many interesting and important discoveries waiting to be explored, but unearthing them requires sustained intellectual investment and an open mind, not simple goal-oriented brute force.

Therefore, we are not saying that scientific progress is generally impossible, but rather that we don't know what will catalyze important scientific discoveries. Just as "disunity" holds surprising value in science, investing in research experiments that seem unimportant but are clearly interesting may also be wise. Though this may mean we first need to traverse many unrelated steps, following interest rather than narrow ambition may better reveal the stepping stones to disruptive scientific discoveries and substantial economic growth.

"Not knowing where you're going" is precisely how information gatherers operate, how treasure hunters search, how stepping stones are collected, the right path to anywhere, the route to the future. "Not knowing where the road leads" is why humans can create great things. Consensus, predictable importance, alignment with national interests — these are all derivatives of goal-oriented thinking, and they only cause us to drift further from what we want as we advance toward the unknown world.

Breaking Free from the Shackles of Predetermined Outcomes

The idea that "disunity" or "unimportance" holds value may sound strange, while goal-driven systems appear perfectly reasonable on the surface. What we want to say is that not all research projects need to set a goal or a research hypothesis. Some projects are worth trying simply from the perspective of interestingness alone.

We could even fund researchers with track records of interesting discoveries without hesitation, much as the MacArthur Fellowship provides substantial funds to highly creative individuals. Of course, the MacArthur Foundation doesn't know where these people's ideas will lead them, and this "blank check" approach may strike you as irrational.

After all, no one knows what these researchers intend to accomplish or how they hope to accomplish it, but the true meaning of scientific research lies in exploring places full of unknowns and uncertainties. If we cannot accept this view, then all paths of "serendipity" without clear goals may be rejected from the outset. Yet as discussed earlier, overly "lofty" goals almost never materialize. Therefore, forcing researchers to state goals in their applications only leads them to propose mediocre objectives.

Fear of risk is a major reason people cling so tightly to goals. But our fear cannot change the fact that risk is an inseparable part of scientific exploration, because scientific exploration requires us to cross many unknown stepping stones over sustained periods of time. Because we hope to go further, risk-averse goal-oriented thinking will limit and constrain our progress.

For example, how many people predicted that advances in consumer electronics would lead to the world's first mass-production all-electric sports car — the Tesla Roadster? Yet by integrating thousands of laptop lithium batteries together, it became possible to create lighter, more powerful practical electric vehicles.

Nothing is more thrilling than the sudden realization that we are just one step away from some unrealized potential. Achievements that once seemed impossible suddenly enter the realm of possibility through previously undiscovered connections. Gradually walking into seemingly unforeseeable dead ends can sometimes yield enormous rewards.

In the long run, it is the accumulation of these stepping stones that brings the greatest innovation. When each small discovery is a revelation, the chain of exploration itself is no less than a revolution. Therefore, while betting on revolutionary discoveries may be high-risk, it will come eventually over time. As with all processes of great discovery, revolutionary discoveries are rarely the goals set by the stepping stones that lead to them. Even if not explicitly stated, investors have long recognized this principle. In short, if you want to invest in visionaries, look for those wandering and exploring in nearby domains of uncertainty.

Indeed, there is a group of innovators who have already seen through the deception of goals to some degree. For artists and designers, the concept behind an idea is often more important than its goal (if one exists at all).

Art tends to focus more on creative exploration than on satisfying a specific concrete goal. Ask any artist, and they'll tell you that in artistic creation, following inspiration's winding path is better than striving to paint the next Mona Lisa.

Of course, when art and design collide, goals can sometimes play a role. In architecture, for example, roofs must keep out rain and foundations must be solid and stable. It turns out these types of goals bear an interesting resemblance to the constraints on organisms in natural evolution. Every living thing in nature must live long enough to survive and reproduce. But different organisms satisfy this goal in various ways, manifesting as the rich and vast diversity of species on Earth.

Thus, rain-proof roofs and stable foundations in architecture are more like constraints on creativity; they are not typical goals in themselves. Just as all organisms must reproduce, buildings must also be functional and safe. Innovation in these domains usually means continually finding new methods within constraints. But the overall search in these fields still pushes into unknown spaces.

Looking back at the history of art and design, we can easily find cases of dramatic and serendipitous chains of stepping stones. In painting, for instance, Impressionism gave rise to Expressionism, which in turn gave rise to Surrealism. Great new directions in art are often discovered precisely because they were not the artist's goal.

Some exploratory steps along this path negate historical steps, while others redefine or modify them. But the important point is that no artist at the outset tries to predict future changes to determine or plan what masterpiece they should create. Regardless of what results it may bring, every artistic innovation has meaning in itself. Meanwhile, the potential to lead people toward newer domains is often the mark of effective innovation.

In current mainstream culture, the idea that progress depends primarily on strict goals has influenced all domains — education, science, art. The way we organize most work seems unable to escape the illusory comfort brought by goal-oriented thinking.

While non-goal exploration itself is not a panacea, we would do well to clearly recognize that blind faith in goal-based exploration and evaluation tends to produce mediocre results, conformity, and subsequent stagnation. Although exploring this world is not easy, because it does not operate simply, at least we know there is a path to break free from the shackles of predetermined outcomes.

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