When should an idea that smells like research be a startup?

When should an idea that smells like research be a startup

Notes about language.

  1. I’m going to be trying to use the word ‘uncertainty’ in the technical sense of* Knightian Uncertainty *that carries a lot more meaning than just “we don’t know.”
  2. I’m referring to things as “ideas” (in the Activity Space sense) to avoid “projects” “programs” etc. because whether it looks more like a project or a program (The distinction between areas, programs, and projects) probably has something to do with whether it makes sense as a startup.

We can say for certain some things about ideas that smell like research:

  1. To some extent they are attempting to do something, usually discovery or invention-wise, that nobody has done before. In other words, they do not have a global Critical path. ^1
  2. They will not be able to generate cash flow directly from their main activities for some amount of time.
  3. As a result of #1, the activity will need some kind of money factory.Innovation orgs need a money factory.
  4. That money factory (or multiple money factories) will need to put money into the idea for some amount of time before it produces a ‘working’ result — a good business, a technology that other people can use, an acquisition etc.
  5. There is unpredictability about the timescale to get to a ‘working’ result. More uncertainty about critical paths means more unpredictability on the timeline, or even the timescale. (Keep the fact that Mismatched Buxton Indexes lead to shear forces in mind.)
  6. In large part because of the timescale unpredictability, there is unpredictability about the amount of money the idea needs to get to that ‘working’ result. Cost is often tightly coupled to the amount of time it takes. Hence, more critical path uncertainty -> more time unpredictability -> more cost unpredictability.
  7. The time and money are necessary to address technology risk (a chance that the technology won’t hit a performance metric) and technology uncertainty (not knowing what the metric actually is).
  8. Researchy ideas have some amount of uncertainty about potential outcomes: what the form of the output will be, whether there is a market for that output, whether the output will be of a form that can capture value from that market, whether the program will organizationally be able to be a business that can do that value capture.

If the idea is housed in a new for-profit organization, #1+#2+#4 means that except in rare cases, the organization needs to be a high-growth startup because in order to provide competitive time-discounted ROI on the money the company needs to do the work over a potentially long timescale, it needs to target massive returns. Being a Grahamian startup then subjects the organization to §Startup Constraints.

One could imagine situations where a for-profit research program could avoid committing to be a high-growth startup. A for-profit could get away with targeting lower growth/eventual value if funding comes from non-dilutive grants or ‘friendly’ investment where the investors don’t expect to make as much return on their money as they could elsewhere. However, both of these options come with their own downsides. These downsides include needing to keep investors happy because ‘friendly’ investment generally means ‘not market competitive’ so investors become much less replaceable. The danger is that the product becomes ‘things that make investors or grant-givers happy’ rather than things that maximize the potential of the idea and push the Knowledge frontier. (Or even make the most money in the long run.) Friendly-funded for-profits also experience a lot of pressure towards efficiency, and Efficiency biases systems towards false negatives. (Of course this efficiency bias is a cultural thing and not tied just to profit-seeking.)

Outliers dominate both the results and these conversations so I’m going to call out the elephants in the room:

  • SpaceX (it’s even debatable whether this counts as an idea that smelled like research — at first they weren’t even trying to do something nobody had done before — there was a pretty clear but very hard critical path).
  • Genentech
  • A number of therapeutic companies
  • OpenAI
  • DeepMind
    The fact that the list is so short compared to the list of researchy for-profits that have failed to deliver on their promises seems indicative. The ‘failure rate’ is even higher than the average for startups. This list also points to the fact that the question might be very discipline dependent. Only SpaceX is the non-therapeutic, non AI company on the list.

At the end of the day, no set of criteria can definitively say “this project shouldn’t be carried forward by a new for-profit organization” except maybe if desired output could never be sold. (Though even then someone could point to profitable but unintended discoveries as a reason for researchy work to be a startup). The nature of Knightian Uncertainty means that it’s certainly possible to flip all heads in a row on a large-dimensional, non-stationary coin and pull off a successful research startup. However, I would argue that the more the unpredictability in each of the steps smells like uncertainty instead of risk (Uncertainty always involves risk but risk does not always involve uncertainty), the less it’s a good idea for the project to be carried forward by a new for-profit organization.

A decision tree may be the correct way to look at the question of whether a program is too researchy to be a startup. These questions are ordered roughly in terms of importance, with “no” answers strongly indicating that a start:

  • Can the desired output be sold?
  • Is there a global Critical path?
  • Is there an objective ‘measure’ of what ‘working’ means? How smooth is it?
  • Is there a bounded amount of market uncertainty?
  • Is the technology a modular product (ie. does it slot into existing systems)?
  • Would investors consider a low ROI acceptable?
  • Would investors be willing to wait a long and unpredictable amount of time to get that return?
  • Are investors ok with an illegible process without clear milestones?

Can the desired output be sold or unlock a product?

If you are setting out to create something that could never be sold, the program probably should not be a startup. There are examples of accidental but profitable discoveries that happened in the course of pursuing something out of motivations besides profit — discovering a heart drug while studying tree frog poison in the amazon for example — but you might as well just buy stocks chosen by a random number generator.

Is there a global critical path?

No global critical path means that you need to run a “fat” process without clear justification. (Justification requires explaining how it fits into a bigger picture which requires a global critical path). Without a global critical path, “progress” is nothing but a narrative and the fat process makes it look like you’re doing a lot of dicking around. As a result, investors will get fed up at some point and either force the research into a premature product or shut the whole thing down.

Is there a smooth objective measure of what ‘working’ means?

One way to look at uncertainty is that there’s no definition of what ‘works’ means: this could be in terms of the technology itself (technology uncertainty) or in terms of how it becomes a good business (market uncertainty). Note that this is different from technology or market risk where you know what winning looks like but there are a lot of reasons why you wouldn’t get there. Uncertainty always involves risk but risk does not always involve uncertainty. Technology risk sounds like “there’s a chance that we can’t get the efficiency of this process above 35% but the back of the envelope says there’s nothing that should prevent that and we have a development plan to get there.” (A metric and a vague sense of a probability distribution over that metric).

Creating new technology will almost always involve some uncertainty. Technology’s modular/combinatorial nature^2 means that there will be uncertainty at some level of the hierarchy. Sometimes that uncertainty will propagate up to the top-level technology if it is an irreplaceable subsystem. However, my extremely hand wavy intuition is that You cannot have massive uncertainty in subsystems without it propagating upwards.

Even if you have a clear measure of what ‘working’ means, the way in which that metric changes matters. A smooth metric means that incremental changes can cumulatively move the needle (which means that you can show nice graphs trending towards success). However, some researchy ideas involve situations where the needle doesn’t move at all until it does a massive jump (ie. They depend on breakthroughs).

Is there a bounded amount of market uncertainty?

Situations where you’re guaranteed a massive market if you can hit a clearly defined target lend themselves to researchy startups. Theraputics are a prime example here^3: “if you can create a cancer drug that passes FDA approval, you are guaranteed a $B market.” In the past, mainframe computers had a bit of this flavor — if you could hit a clear performance metric, you had a guaranteed market. It is possible that healthtech and therapeutics in the early 2020s is to biotech what calculation and mainframes were to computers in the 1960s.

A big reason that market uncertainty can kill researchy startups is less about investment and more about the fact that There is a tradeoff between an organizational culture that is good at addressing market uncertainty and one that is good at addressing technological uncertainty. At some point a researchy startup needs to do a dramatic gear shift into growth and product-market fit mode. This transition often either prematurely kills the research potential or the company dies because it’s being run by people with a research mindset.

Is the technology a modular product (ie. does it slot into existing systems)?

Startups are good at point changes. If there is a component in a system that can be improved or swapped out in order to make the system cheaper/more profitable/more efficient, startups are an excellent mechanism for making that happen. The same goes for projects in industrial research labs — if you can, say, save the company a ton of money by swapping out the sheathing on telephone cables, the path to success is straightforward. However, to improve, many systems need many simultaneous changes (or to be swapped out for a new process entirely^4).

Systems must take performance hits to get out of local optima and people are rarely willing to pay to decrease system performance. (This is a major contributor to The (idea) valley of death).

See also Systems research requires a lot of work that is expensive and uninteresting

Would investors consider a low ROI acceptable?

A lot of research involves dicking around, or “fat” processes. If you need to target a high ROI from day one, you need to be as efficient as possible. ROI is all about efficiency, and Efficiency biases systems towards false negatives. There will just be less Slack - concept in the system, cutting off lines of work that can’t be justified up front (especially if they require resources to evaluate).

Would investors be willing wait a long and unpredictable amount of time to get that return?

A key characteristic of research is that regardless of how long it takes, that amount of time is unpredictable.^5 Combined with the fact that progress is often not smooth, it takes a constitution of steel for investors not to start getting antsy at some point. People are patient until they’re not. The pressure to show some progress towards a progress makes sense from a business sense but can be at odds with developing a powerful technology. Premature specialization is a common failure mode in researchy startups. (Ideally corporate R+D enables work on a general purpose technology before it’s specialized) .

Are investors ok with an illegible process without clear milestones?

In addition to unpredictable timelines, a lot of technical research involves constantly shifting targets. You can set milestones (and it is often useful to do so), but they need to be incredibly fluid. Unlike business progress, which can be boiled down to a few core metrics like customers or revenue regardless of how much pivoting is happening, research progress is much harder to boil down to a legible metric.

Some questions that are proxies for the degree of technological uncertainty facing a project:
How smooth is the technology’s fitness landscape? That is, how much could a single change shift outcomes?
The smoothness of a technology’s fitness landscape has a big effect on a program’s technological uncertainty
Do you know what it means to improve?

Do you know how you will know that you know how to incrementally improve the system?



^1: In other words, they are not in the lower left quadrant of raoGUTSGrandUnified2018
^2: See arthurLogicInvention2005
^3: See Therapeutics have established sales channels
^4: See fillerFundamentalManufacturingProcess2020
^5: See narayanamurtiCyclesInventionDiscovery2016

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