Important problems lead to important work.

10/11/23   |   Written by Daniel Goodwin, Paul Reginato, Paul Himmelstein, Ariana Caiati

What is the most important problem of your field?

Richard Hamming made himself unpopular at the lunch table of Bell Labs.

In the 1950s, Hamming became bored of his normal mathematician lunchmates and joined the chemist’s cafeteria table. He insisted on asking people what the most important problems of their fields were and then followed up with “well, are you working on them?” The chemists took offense to his blunt observation that if you don’t work on important problems, you’re unlikely to do important work. While most ignored his provocations and ejected Hamming from the table, a few people listened. Dave McCall, for one, had his career take a sharp turn upward: he became department head, then national academies member and a winner of posthumous chemistry breakthrough prize.

Some might say it’s just the idealism of a mathematician within a monopoly-funded research lab that would have the privilege to say “hey just go work on the most important problem in your field.” But what if we took Hamming’s optimism to heart and focused on helping people identify and pursue the most important problems?

A great problem can fire up a field if it is convincing and actionable. Because climate biotech does not yet have a list of Most Important Problems, we designed the Garden Grants to encourage scientists and technologists to frame their own problem as part of the grantmaking process. This is a respect to the knowledge of the practitioners in the climate biotech community: we simply require that protein engineering is involved for this round of Garden Grants. The Garden Grants process is a $1 Million experiment to show that grantmaking can strengthen a community by surfacing problem statements that diverse teams want to tackle. This experiment will only succeed if the problem statements are written to a high degree of quality.

Let’s go through a brief history of problem statements, touch on the solution statement, then end with how it will work with our platform partner,

The history behind crafting a good problem

A good problem statement motivates the reader to care about the solution. So what makes a good problem and what is the best way to communicate it?

Such a question may sound pedantic but it’s a deep question with a long history. For brevity, we can focus on two leading perspectives: Richard Hamming of Bell Labs and George Heilmeier of DARPA.

The opening story of Hamming at the lunch table comes from his famous lecture “You and Your Research.” It’s one of those seminal works that most scientists say they wish they had read earlier in their careers. We take for granted that much of science is driven by funder-led problem statements (eg, NSF RFPs), in which the funder defines the problem important to them. Funder-led priorities have become the dominant paradigm for a reason over the past few decades. But if we want to encourage a culture of high-agency scientists surfacing problems from their expertise, there must be a language for convincing the funding sources of a problem’s importance.

Potential impact is not enough to make a good problem. Hamming expands on his definition of importance to say that a problem must have a valid attack (ie, be actionable):

Let me warn you, ‘important problem’ must be phrased carefully. The 3 outstanding problems in physics, in a certain sense, were never worked on while I was at Bell Labs. By important I mean guaranteed a Nobel Prize and any sum of money you want to mention. We didn’t work on (1) time travel, (2) teleportation, and (3) antigravity. They are not important problems because we do not have an attack. It’s not the consequence that makes a problem important, it is that you have a reasonable attack. That is what makes a problem important. When I say that most scientists don’t work on important problems, I mean it in that sense.

Antigravity: a world-changing result if possible,but lacking any serious path to attack in Hamming’s time. (An artist’s depiction taken from the Wikipedia page for Antigravity)

Similar to Hamming’s notion of an attack on a problem, in the 1970’s George Heilmeier created the rubric of problem quality in DARPA. Now known as the Heilmeier Catechism, it is still the standard rubric for deciding if a project is worth undertaking. It’s a simple set of 8 questions, including

  1. “What are you trying to do? Articulate your objectives using absolutely no jargon”
  2. “How is it done today, and what are the limits of current practice?”
  3. What is new in your approach and why do you think it will be successful?
  4. Who cares? If you are successful, what difference will it make?

Good protocols have a layer of obviousness to them. The Heilmeier Catechism stuck because of its usability by both people presenting an idea and evaluating an idea. In some sense, this is DARPA’s equivalent for Silicon Valley’s “elevator pitch” thought experiment (refer to our first blog post for Garden Grants). We tried a few different versions, including Hamming’s and Heilmeier’s approaches, but climate biotech needed something different.

From the frontier to tangible: problem statement structure for Garden Grants

When designing Garden Grants, we wanted problem statements to define granular, actionable problems while clarifying how they relate to frontiers in sustainability. As we set out to choose a format, we were fortunate to find that our platform partner for Garden Grants,, had gone through their own process of problem statement structure that matched Homeworld’s priorities.

As a crowdfunding platform, Experiment solicits funding from general readers, so it must facilitate communication of why a niche-sounding science project is relevant to issues of general interest. Experiment has a three-part statement for Context, Significance, and Goals. The sections together form a chain of reasoning that motivates a specific project, providing the opportunity to criticize or further investigate any part.

We limit each section to 800 characters. We know a 2400-character (~¾ page) document is too short to fully articulate the intricacies of a problem but it can act as the equivalent to the startup’s elevator pitch. It must indicate the frontier goal (context), the actionable subproblem (significance) and what target endpoints could be (goals).

Illustrating a problem statement with carbonic anhydrase

Let’s explore how a problem can be communicated using the context-significance-goals framework. As an example, we’ll use this problem statement about engineering ultrastable carbonic anhydrase for catalyzing CO2 absorption in direct air capture (DAC). It is one of several problem statements we’ve shared in our Problem Statement Repository that are derived from our roadmapping work on the same topic (report, summary).

You can also see what this would look like as an application on

Structure of carbonic anhydrase, one of nature’s effective enzymes (PDB: 1cnw).


Guideline: The Context frames the big picture. It describes a challenge important to society and a constraint that limits us from addressing the challenge. However, it is too broad to imply the goals of a specific project.

Example: “Atmospheric CO2 removal (CDR) and point-source capture (PSC) of CO2 are well-accepted as being necessary for successfully decarbonizing within climate goals (1). Direct air capture (DAC) is a CDR pathway with ideal verifiability and durability. Both DAC and PSC are cost constrained, primarily by the CapEx of the gas contactor and the energy required to drive large swings in temperature or pH to regenerate CO2 from the capture material (2).

Those high cost and energy requirements are driven by a thermodynamic trade-off between the rate of CO2 absorption and the CO2 regeneration energy: CO2 capture materials with high absorption rate, which reduce cost by reducing the gas contactor size, typically have high CO2 regeneration energy, and vice versa (3).”

Analysis: In this example, the Context begins by describing the need for carbon dioxide removal (CDR) and point-source capture as carbon management technologies. It motivates DAC as a CDR technology that has some ideal features but is cost-limited. It then articulates the reason why DAC is cost-limited: a thermodynamic trade-off inherent to most capture materials. At this point, we’ve defined a problem – developing a capture material without the trade-off – but that problem can be made much more actionable by providing a more granular problem focused on the capture material itself.


Guideline: The Significance describes a possible pathway to address the constraint described in the Context. It then describes another more specific constraint that prevents progress on that pathway, to be addressed by the Goals.

Example: “Carbonic anhydrases (CAs) catalyze fast CO2 absorption in solvents with low CO2 regeneration energy, resolving the tradeoff described above (4). CA could reduce DAC and PSC cost by reducing parameter swing size or gas contactor size, if it were stable in DAC or PSC processes that may include high pH, temperature, or ionic strength. E.g., thermostable CA via protein engineering (PE) can already reduce PSC cost >30% (5,3).

AI-driven PE and screens of many natural variants are revolutionizing PE but haven’t been applied to CA. Ultrastable CAs produced using those tools likely could reduce DAC and PSC cost substantially. While modeling is needed to quantify application-specific benefits and target CA properties, PE for ultrastable CA can begin now and later be adapted to specific uses.”

Analysis: Here, the Significance begins by introducing a possibility by which the enzyme carbonic anhydrase (CA) could resolve the thermodynamic trade-off that constrains DAC and PSC, as described in the Context. It then introduces a new constraint, which is a lack of stability of CA in the capture solvents used for DAC and PSC. It points to next-gen protein engineering as a way to address the stability. This example notes that modeling is needed to resolve uncertainty around the specific target properties of engineered CA and the quantification of potential benefits, but claims that protein engineering of CA can begin now and then be adapted as specific targets are revealed. It also links to another problem statement describing the need for modeling. This section would be stronger if the specific performance requirements of CA could be described, but it honestly acknowledges the uncertainty.


Guideline: The Goals describe a set of project outcomes that address the specific constraint described in the Significance and are achievable by one person or a small team. The Goals might seem esoteric on their own, but the Significance and Context clarify why they are important in the big picture.

Example: “While modeling analyses are ultimately required to provide target properties for ultrastable CAs to be used in development of novel CA-enhanced DAC and PSC, initial efforts to use AI-based PE and screens of many variants should target many-fold CA stability improvements compared to the state-of-the-art while retaining high activity (kcat/kM ~108 M-1s-1). For a comprehensive discussion of state-of-the art CA engineering and performance, see (6) and (4).

Example stability benchmarks are:

  • temperature stability:
    • 203-day half-life at 60 ˚C (7),
    • 73% activity retention after 24 hrs day at 80˚ C (4,8)
  • pH stability:
    • 90% activity retention after 24 hrs at pH 11.0 (9)
  • Stability demonstrations should be performed in solvents relevant to DAC and PSC, such as 10-20% K2CO3.”

Analysis: This example acknowledges the need for modeling work to provide a clear set of target CA properties, and then submit “many-fold improvement over specific state-of-the-art” as an initial target for protein engineering now, while other work is still pending. The state of the art is cited specifically. Again, these Goals would be strongest if they prescribed quantitative targets that fully addressed the constraint described in the significance; however, it is good that they openly acknowledge the uncertainty in the targets and still give a clear set of outcomes that can be pursued in a single project.

Good problem statements build interest and dialogue

A successful problem statement turns heads. It highlights a subtle challenge, surfaces an overlooked opportunity for impact and welcomes future collaborators. In the context of Garden Grants, an excellent problem statement is the first step towards receiving funding.

Garden Grants is itself an experiment to show that it is to the researcher’s benefit to put their interests public. In the best case, it will help encourage practitioners to work on the important problems for which Hamming would approve.

We hope the presence of the Garden Grants empowers you to imagine the “Hamming Problems” involving protein engineering’s potential in climate.

By Daniel Goodwin, Paul Reginato, Paul Himmelstein, Ariana Caiati