Three Schools, Three Shocks

Physics, system, and industry have each asked their own question of life. Three times a discovery let all three ask it at once. The third time stalled, and the reason is narrower than it looks.

Fangzhou Xiao · BioMAC Lab, Westlake University · 17 August 2026 · companion to The Biomachine Perspective

1Three questions, not three fields

Physics asks what life is as an object. System asks how life works as a machine. Industry asks how life could be useful as a tool.

These are not three disciplines. They are three questions, and each has its own idea of what would count as an answer.

The physics question wants an invariant. Something true of life the way thermodynamics is true of gases: a bound, a scaling, a law that does not care which organism you brought. The systems question wants a reason. Given that a cell does X, why is it built this way and not the other way, and what would go wrong if it were? The industry question wants a yield. Given that we want Y, what do we feed the cells and what do we change in them.

Because the answers look so different, the three schools can work in the same building for decades without meeting. What makes the history interesting is that three times they were forced to meet, each time by a discovery that made the same object visible to all three at once. What follows tracks those three meetings, and then argues that the third one broke down for one identifiable technical reason.

2The questions are old, and the answers are borrowed

Each school's ancient form is not a quaint prelude. It is the same question with a worse vocabulary.

Take the systems question first, because its pattern is the clearest. "How does life work as a machine" has always been answered by reaching for the most impressive machine available. Life works like fire, an elemental transformation. Like a system of fluids, so that draining some blood might rebalance it. Like a pump, once Harvey had one. Like a clockwork automaton, once Descartes had one. Like a steam engine, once there were engines. Like a servo loop, once there were servos. Like a circuit, then a computer, then a neural network.

It is tempting to read this as a series of mistakes. It is better read as a series of instruments. Each machine metaphor imports a whole analytical apparatus along with the image, and the apparatus is what does the work. When Cannon named homeostasis and Wiener named cybernetics, the payload was not the word but the mathematics of negative feedback. The cost is that you also import the metaphor's blind spots, and those are invisible from inside. That is precisely the trap Part IV is about.

That is worth pausing on. The two ideas this whole history turns on, that life is a machine and that life is chemistry all the way down, were canonised together, in print, by one of the architects of molecular biology, in 1970 and 1971. Monod's table of contents is the outline of the next fifty years.

The physics question has the same borrowing pattern with a different flavour. Its answers are attempts to name what kind of object life is: a form, a flow, a vital fluid, and then, once statistical mechanics existed, an ordered structure that resists the second law. Schrödinger's aperiodic crystal is the famous instance. What matters is the move, not the answer: pick a class of physical object, and see what follows from life belonging to it.

The industry question is the oldest of the three and the least troubled by any of this. Beer, wine, soy sauce, fermented fish, bread, cheese, the harnessed horse. All of it is life put to work with no theory of life at all. This is the school with the longest unbroken record of success, and it is the school least dependent on the other two. Remember that when we get to §17. When the theory-driven programme stalled, the field did not collapse. It fell back on the school that never needed the theory.

3What the 1970s actually settled

The thesis was old. What was new was that you could now name the enzyme, write the reaction, and cut the DNA.

The 1970s are remembered as the decade the universality of biochemistry became a foundational consensus. The shape of that is right and the date needs care, because the intellectual content was won much earlier, in stages. Wöhler synthesised urea in 1828. Buchner fermented sugar with cell-free extract in 1897. Sumner crystallised urease in 1926 and enzymes became proteins. Watson and Crick in 1953. The genetic code closed by 1966. By any reasonable reading, "life is chemistry" was settled science before 1970.

So why does the 1970s feel like the moment? Three things converged, and none of them is the thesis itself.

1. The last big mechanism closed. Mitchell's chemiosmotic hypothesis, proposed in 1961 and resisted for a decade, carried the field through the 1970s and took the 1978 Nobel. With oxidative phosphorylation explained, bioenergetics had no remaining place for anything but chemistry.
2. The toolkit became universal. Restriction enzymes (1978 Nobel), recombinant DNA in 1972 and 1973, Asilomar in 1975, Sanger and Maxam–Gilbert sequencing in 1977. Chemistry stopped being only an explanation and became an intervention.
3. The thesis got written down by its architects. Monod's Chance and Necessity (1970 in French, 1971 in English) and Jacob's La logique du vivant (1970) are the canonical statements, and they arrive precisely at the turn of the decade.

4Physics: kinetic proofreading

Take an equilibrium bound seriously, notice the measured value violates it, and conclude that something must be burning fuel.

This is the cleanest example in biology of the physics move. Here is the argument as Hopfield states it.

Discrimination between a correct substrate C and a near-identical wrong one D happens at a recognition site that makes the pathway energetically more favourable for C. In a simple scheme, the error frequency is bounded below by exp(−ΔG_CD/RT), where ΔG_CD is the largest free energy difference available along the path. That bound is a thermodynamic statement, and it is not negotiable.

Now put in the measured numbers. Protein synthesis inserts the wrong amino acid at most about 1 in 10⁴ times. To buy that from a single equilibrium discrimination you need 5.5 kcal/mol, which Hopfield says is "often difficult to justify" for codon–anticodon binding or amino acid recognition. DNA replication is worse: the error rate is about 10⁻⁹.

The resolution: if the reaction is "strongly but nonspecifically driven, e.g., by phosphate hydrolysis", the same discrimination step can be applied twice, and the error becomes the square of the equilibrium floor. Two facts about this deserve emphasis. First, the mechanism is forced by the contradiction, not fitted to data. Second, Hopfield notes that the scheme he is displacing is "based on Michaelis kinetics", so the physics critique lands squarely on a Michaelis-kinetics account of the mechanism. Hold that thought until §19.

Ninio, and what "independently" means

Ninio's paper is real, contemporaneous, and different. It was submitted 12 December 1974, four months after Hopfield's 6 August 1974 contribution, from the Salk Institute, and published in Biochimie in 1975. Its own summary says it discusses "the relationship between our scheme for a delayed reaction and Hopfield's scheme", citing Ninio's own prior scheme in a CNRS volume then in press.

The nuance that matters: Ninio's argument is probabilistic and kinetic, framed as a "kinetic amplifier" arising from a delay in one step. He does not make the thermodynamic-contradiction argument. So "discovered independently" is fair on priority, and "the same argument" is not. Hopfield brought the physics. Ninio brought the mechanism-space analysis. It is a useful reminder that the two temperaments coexist even inside a single school.

5System: demand theory and the inverse problem

See a design, ask what function it is optimal for, and let the answer be checkable against a census of real operons.

The systems move needs a target, and Savageau found an unusually clean one. A cell must turn a gene on when a signal is present. Two architectures do that. Activate an activator, or de-repress a repressor. Functionally they are interchangeable. So why does nature use one here and the other there?

The methodological problem is stated exactly in the 1977 paper, and it is the heart of the systems school.

The model is the instrument that makes the controlled comparison possible. That is the systems school's characteristic use of theory, and it is worth naming because it is not prediction. The model holds function fixed so that architecture can vary.

And the answer, in the paper's own words: regulation by a repressor is selected when there is low demand for expression in the organism's natural environment, and regulation by an activator when there is high demand. Use it or lose it.

The reasoning behind that rule is the interesting part, because three candidate objectives are eliminated before the surviving one.

Two refinements the full texts force.

The population argument is present in 1977, but qualitative. The 1977 paper argues through the fate of regulatory mutants and their "selective disadvantage". The explicit population-dynamic model, with mutation rates and growth rates for wild type and each mutant class across two environments, is the 1998 quantitative development. Both are in Part I and Part II of the 1998 pair.

The rule is contested, in a productive way. Gerland & Hwa (2009) examine how far the lethality assumption holds and find regimes where individual-level robustness dominates instead. Shinar, Dekel, Tlusty & Alon (2006) derive a related rule from error minimisation, and Sasson et al. (2012) tie mode of regulation to insulation of expression. The rule survives. Its unique explanation does not.

6Industry: the cell as a chemical plant

One idea, two programmes, two decades, and two opposite attitudes to rate constants.

The cell-as-chemical-plant move is usually placed in the late 1970s and early 1980s, producing flux balance analysis and metabolic control analysis together. It splits cleanly into two distinct programmes, with different mathematics and different decades.

Metabolic control analysis is 1973–74, and it is about sensitivity. Kacser & Burns and, independently, Heinrich & Rapoport asked how a change in one enzyme's activity propagates to the flux through a whole pathway. The answer is the control coefficient and the summation theorem, which say that control over flux is distributed and sums to one. This is a physiology question answered with calculus, and its most famous downstream consequence is Kacser & Burns's structural explanation of genetic dominance.

Flux balance analysis is the mid-1980s, and it is about stoichiometry. Varma & Palsson's 1994 review, which is the consolidating statement, traces the lineage to Papoutsakis 1984 on butyric-acid fermentations, Fell & Small 1986 on fat synthesis under stoichiometric constraints, and Watson 1984 and 1986. The framing is unmistakably industrial: "Flux balance methods only require information about metabolic reaction stoichiometry, metabolic requirements for growth, and the measurement of a few strain-specific parameters."

The engineering discipline that grew from this was named by Bailey in 1991 as metabolic engineering, and codified in Stephanopoulos, Aristidou & Nielsen (1998). Bailey's own 2001 commentary is worth reading against this whole document, because it draws the distinction the rest of the argument turns on: the information needed to predict a biological system's behaviour splits into the systems-structural (which components, and which interactions among them) and the parametric (the rate constants and equilibrium constants). His bet was that structure carries much more than people assumed. Part V is an argument that he was right, and that the field bet the other way.

7What the genome bought

Not new physics. A complete parts list, which is a different and in some ways more dangerous gift.

In the 2000s it became possible to see the whole cell, and that licensed a new level of ambition in all three schools. The mechanism is worth being precise about, because the parts list is exactly what makes the third shock's disappointment intelligible.

A sequenced, annotated genome gives you three things. An enumeration of the components. For metabolism, the stoichiometry of nearly every reaction, because gene annotation names the enzyme and the enzyme fixes the reaction. And a coordinate system in which to place measurements, which is what made the omics era possible.

What it does not give you is any rate law, any binding constant, any copy number, or any indication of which reactions matter under which condition. The genome delivers the structural half of Bailey's split and none of the parametric half. Every programme in this part is an attempt to get by on the structural half, and the differences between them are differences in how they handle that gap.

8Physics meets system: chemotaxis, end to end

One pathway followed from receptor to flagellar motor, with a system-level property proved to be architectural rather than tuned.

Chemotaxis is the culmination of the 1999–2000 moment, and the best-documented episode in the whole story. The sequence is worth laying out because it is a template.

1. Behaviour, quantified. Berg & Brown 1972 track single cells in three dimensions. Segall, Block & Berg 1986 measure the impulse response and find its integral is zero. Adaptation is a measured fact, in 1986.
2. The property is claimed to be robust. Barkai & Leibler 1997 argue that exact adaptation cannot come from parameter tuning, because it survives parameter variation.
3. The claim is tested. Alon, Surette, Barkai & Leibler 1999 vary CheR expression over a 100-fold range. Adaptation time moves more than 20-fold, from 23 ± 2 minutes down to about 1 minute. Adaptation precision stays flat. One property is structural. Its neighbours are fragile.
4. The structure is named. Yi, Huang, Simon & Doyle 2000 identify methylation as an integrator, with CheR and CheB saturated, and invoke the internal model principle: perfect adaptation if and only if integral feedback.

That is the physics school and the systems school doing one job. Step 3 is a physicist's move, distinguishing a robust observable from a tuned one. Step 4 is a control engineer's move, matching a measured invariance to a theorem about architecture. Neither is possible without the parts list, because the theorem is about the whole loop from receptor to motor.

9System meets industry: the VLSI roadmap

The founding papers used Hill functions. The founding manifesto cited the VLSI textbook by name. Both facts matter later.

Two papers in Nature in January 2000 started the engineering programme. Elowitz & Leibler built the repressilator, three repressors in a cycle, and Gardner, Cantor & Collins built the toggle switch, two mutually repressing genes.

Both are modelled with Hill functions, and the details are worth having exactly, because they come back in §20.

So the field's dynamical vocabulary was fixed, from the first week, as Hill functions composed additively. Now the second half of the roadmap.

Endy's 2005 manifesto is the programmatic statement: standardisation, decoupling, abstraction, so that biology can be engineered the way other things are engineered. It cites Mead & Conway, Introduction to VLSI Systems, Addison-Wesley, 1980 by name, and the lesson it draws from that book is specific. Decoupling is illustrated by "very-large scale integrated (VLSI) electronics, which is an engineering technology that only became practical once rules were worked out to enable the separation of chip design from chip fabrication".

That provenance is not Endy's alone. Way, Collins, Keasling & Silver (2014) record that the framework came out of a 2003 DARPA-sponsored study which "resulted in a recommendation that the field of synthetic biology should learn from the earlier developments in the microchip industry", explicitly including MOSIS and the separation of design from manufacturing.

Two details in the manifesto are worth extracting, because later sections are about their failure.

Endy also noticed, correctly, the one curve that did behave: "Bulk DNA synthesis capacity appears to have doubled every 18 months or so for the last ten years." That trend continued for another two decades. The design layer built on top of it did not. Figure 7 is that contrast.

It is worth being fair to the analogy, and the fair point deserves more than a concession. A resistor is not a law of nature. It is a manufactured object whose linearity is the product of decades of materials work, and the same is true of a transistor with a clean transfer curve. The 2000s programme was not wrong to want components. It was wrong about what stage of the process it was at. Electronics had its abstraction because someone first built the parts that deserved it.

10All three at once: genome-scale metabolism

The parts list plus stoichiometry plus linear programming, and a real prediction accuracy to report.

Edwards & Palsson (2000, PNAS) is the moment the industrial school cashed the genome. The annotated E. coli MG1655 sequence plus biochemical information gives a genome-specific stoichiometric matrix, and that matrix plus capacity constraints defines the space of achievable flux distributions. They then knock out genes in central metabolism, in silico and in vivo, and compare.

The number is 86% of examined cases predicted qualitatively correctly for growth or no growth. That is a real, checkable, useful result, and it was obtained with no rate laws at all. The refusal of kinetics was a strength here.

It is also the ceiling. A stoichiometric model can tell you what is impossible and what the best conceivable yield is. It cannot tell you what a cell will actually do, when, or how fast, because those are the questions kinetics answers. Orth, Thiele & Palsson (2010) are clear about this in the canonical primer, and §16 returns to what the ceiling has meant in practice.

11The fourth programme: growth laws

Copenhagen, not Amsterdam. Salmonella, not E. coli. Exponential in 1958, linear in the right ratio by 2010. And it matters more to this story than it looks.

The story usually told is that a Maaløe-era group showed RNA fraction is linearly proportional to bacterial growth rate across media, that the thread went quiet, and that Hwa picked it up in the 2000s with omics tools. The shape is right. Four details are wrong, and one of them changes the argument.

Now the part that changes the argument. Scott et al. 2010 is not a side thread. Read its abstract as a document about synthetic biology, because that is partly what it is.

That last clause is a complete research strategy, and it is a rival to the one argued for here. Hwa's answer to "we have no foundational model class" is: do not wait for one. Find phenomenological laws that hold across conditions, and use them. It worked. The linear growth law, overflow metabolism, proteome partition, and the quantitative response to translation-inhibiting antibiotics all came out of it, and Klumpp, Zhang & Hwa (2009) turned it directly on the gene-expression side effects that were about to blindside the circuit engineers.

So the correct account of the 2000s has four programmes, not three, and the fourth had a different theory of what theory is for. §22 puts it side by side with the others.

12Dating the turn

The plateau was measured in 2009 and named in Nature in January 2010. What 2012 to 2016 added was not the diagnosis but the numbers.

The cooling is usually dated to roughly 2013–2016. That is right about when the quantitative evidence landed, and about three years late for the diagnosis. The turn has three dates, not one, and the first is the one that matters most.

2009, the measurement. Purnick & Weiss counted regulatory regions per published circuit from 2000 to 2008, found a plateau, and proposed that the design principles were too simplistic. §18 treats this as the central piece of evidence in the whole story. Everything that follows in this part is the field working out why that plateau was there.

2010, the year it went public and the year the field split. Two things happened, both in Nature, pointing in opposite directions. In January, Kwok's news feature "Five hard truths for synthetic biology" reported the plateau as news and enumerated the reasons. In December, Elowitz & Lim published "Build life to understand it", which reframes the entire enterprise.

Kwok's five truths deserve to be listed in full, because four of them are the entire diagnosis this essay reaches, and because they were in print in January 2010.

And the reframing, from two of the field's most prominent circuit builders, in the same year:

So the field's justification inverted, from "understand biology in order to engineer it" to "engineer it in order to understand biology". The inversion has a precise date: December 2010, in a Nature comment, argued for on the merits rather than as a retreat. Note also that Khalil & Collins published "Synthetic biology: applications come of age" in the same year, saying the opposite. 2010 is the year the field split on whether it was delivering.

There is one genuine complication, and it is worth more than the tidy version. The field's own histories do not agree on when the trouble was. Cameron, Bashor & Collins (2014) divide the field into four periods, and their label for 2004 to 2007 is "expansion and growing pains", "characterized by an expansion of the field but a lag in engineering advances". Their label for 2008 to 2013 is "increase in pace and scale". So Collins's group puts the lag before Purnick & Weiss measured it, and calls the years usually identified as the cooling an acceleration.

2012 to 2016, the quantification. This is where the usual dating is right, and the next five sections are that evidence. What arrives in these years is not a new insight. It is measurement: how far off composition actually is, how much a circuit actually costs its host, and how fast an unburdened design is actually lost to evolution.

13The parts do not compose

12,563 promoter and ribosome-binding-site combinations, measured. The conclusion the authors drew was to stop predicting.

The single most decisive paper is Kosuri, Goodman, Cambray, Mutalik, Gao, Arkin, Endy & Church (2013, PNAS). Note that author list before reading the result. Arkin, Endy and Church, three of the architects of the standardisation programme, are on the paper that measures whether standardisation works.

They synthesised 12,563 combinations of common promoters and RBSs and measured DNA, RNA and protein for the whole library at once. Against a simple multiplicative model:

The most important sentence in Kosuri et al. is not a number. It is the conclusion:

Read that against Endy 2005. The 2005 programme was standardisation so that composition would be predictable. The 2013 verdict, from partly the same people, is that composition is not predictable enough, so build a library and screen. The field did not merely find composition hard. It changed strategy away from prediction.

The companion papers from the same BIOFAB collaboration, Mutalik et al. (2013a) and (2013b), are the constructive answer, and the full texts sharpen the point rather than softening it. Two numbers side by side.

That pattern is worth naming, because it recurs. Faced with a composition failure, the field's successful response has repeatedly been to build a physical insulator rather than a better model: bicistronic designs here, insulating load drivers for retroactivity in §15, copy-number-invariant promoters for plasmid variation, orthogonal ribosomes for host coupling. Each works. None of them composes, in the sense that none makes the next circuit predictable.

The field also has a precise name for what is missing here, coined by four of its leaders. Way, Collins, Keasling & Silver (2014) propose distinguishing concept modularity from engineering modularity:

That is the sharpest available statement of "genes turned out not to be modular", and it locates the failure correctly. The gene is a real conceptual unit. It is not an interface with a defined signature. The same paper adds an observation that explains why some things are composable: the modularity of operons and pathogenicity islands "is a consequence of natural selection", because those units were selected for horizontal transfer between hosts. Where biology is modular, selection put the modularity there. It is not a generic property of genes, and it is not guaranteed to sit where a designer wants a boundary.

14The host is not a chassis

Put a circuit in a cell and the cell pushes back. Six independent measurements of the same fact, against an assumption the field wrote down in 2005.

The 2000s picture was that a wild-type cell is a chassis, and the circuit is what you bolt on. That picture inverted, and the chassis turned out to be doing the work. This is the one place where the assumption was written down explicitly at the start, which makes the test unusually clean. Endy 2005 defines the chassis as a cell providing resources "to any engineered biological system placed within the cell, independent of the details of the system". Every result below measures a dependence on the details of the system.

Here is the evidence, in increasing order of how much it hurts the modular picture.

1. Expression costs capacity, measurably. Ceroni, Algar, Stan & Ellis (2015) built an in vivo capacity monitor and used it to rank constructs by burden. Their framing: "all heterologous expression represents an unnatural load, consuming cellular resources and leading to decreased growth rates that can predispose synthetic constructs to evolutionary instability." Growth burden and mutational escape are the same problem seen at two timescales.

2. Two unconnected genes are quantitatively coupled. Gyorgy et al. (2015) put one constitutive and one inducible reporter on the same plasmid, with no regulatory path between them, and found the attainable pairs of protein concentrations constrained by a linear relation. They call it an isocost line, borrowing from microeconomics. Changing the inducible gene's RBS strength rotates the line. Changing plasmid copy number shifts it.

3. The coupling can invert a circuit's function. Qian, Huang, Jiménez & Del Vecchio (2017) built a library of genetic activation cascades and tuned each gene's resource demand explicitly. Resource competition creates "non-regulatory interactions among genes", and in an activation cascade these produce responses that are "biphasic or monotonically decreasing". An activation cascade that goes down when you induce it is not a mis-tuned module. It is a module whose sign is not its own.

4. Growth itself is a feedback loop through the circuit. Tan, Marguet & You (2009) found bistability emerging from a circuit that has no bistable motif, purely because expression slows growth and slower growth dilutes less. Klumpp, Zhang & Hwa (2009) had already worked out the general growth-rate dependence of gene expression from the physiology side.

5. Past a threshold, both the circuit and the cell collapse together. Nikolados, Weiße, Ceroni & Oyarzún (2019) coupled circuit models to a host resource-allocation model and found the coupling is not gentle. Increasing induction buys protein output at the cost of growth, but only up to a point: "cellular capacity reaches a tipping point, beyond which both gene expression and growth rate drop sharply", from ribosomal scarcity. Their conclusion is that burden can "limit, shape and even break down circuit function". A design margin that assumes graceful degradation is the wrong margin.

6. Evolution deletes what it cannot afford. Sleight & Sauro (2013) evolved 192 populations of randomised three-colour circuits and read stability off directly. Circuits expressing below 10% of maximum were significantly more evolutionarily stable, which they read as a fitness threshold for retaining a circuit at all. Note what this does to the design problem: the usable region is bounded above by burden, and burden is set by the rest of the cell, so the specification cannot be written for the circuit alone.

Cardinale & Arkin (2012) is the paper that named this class of problem and tried to classify it. Their opening sentence is the field's mood in one line: despite the effort spent designing biological processes that follow predetermined rules, "their operation remains fundamentally circumstantial."

15Retroactivity, honestly

It is often waved away as trivial. That is half right, and the half that is wrong is the important half.

Retroactivity, from Del Vecchio, Ninfa & Sontag (2008), is the back-action of a downstream module on its upstream driver. A transcription factor that regulates a downstream promoter must bind it, and bound molecules are not free, so the downstream load changes the upstream signal.

The standard objection is that this is obvious. Of course binding titrates the input. Calling it a deviation from modularity dresses up bookkeeping as a discovery.

The objection has force, and the mechanism really is that simple. But two things make it more than bookkeeping, and both are worth conceding before §19 uses them.

First, the effect is measured and it is large. Brewster et al. (2014) and Lee & Maheshri (2012) show that decoy and competing binding sites reshape regulatory input functions substantially, in bacteria and yeast respectively. Whether or not it is conceptually surprising, it is quantitatively decisive.

Second, and this is the part the "it's trivial" reading understates: it is a failure of the input–output abstraction, not an error in a parameter. If a module's transfer function changes when you attach a load, then a module does not have a transfer function. No amount of better parameter estimation repairs that, because the object being estimated does not exist independently of its context. This is exactly why the field's response was engineering rather than measurement: retroactivity attenuation, load drivers, promoters engineered for copy-number invariance. Those are attempts to build the conditions under which the abstraction becomes true, which is the correct response and is precisely what electronics did with resistors.

16The models did not become design tools

Whole-cell models turned out to be excellent at something other than prediction, and the honest version of that is more interesting than "they failed".

Karr et al. (2012) built a whole-cell model of Mycoplasma genitalium accounting for every annotated gene function. Its claimed successes are real and specific: in vivo rates of protein–DNA association, an inverse relationship between the durations of replication initiation and replication, and previously undetected kinetic parameters found by experiments the model directed.

The usual verdict on such models is that they do not really predict much and are not much use for guiding experiments. The full texts support a sharper and less dismissive statement. Look at what Macklin et al. (2020, Science) actually report for E. coli.

The finding is that the literature's own parameters are mutually inconsistent, and the whole-cell model is the instrument that detects it. That is a consistency checker on the field's measurements, which is genuinely valuable and is not what anyone was promised. Ahn-Horst et al. (2022) continue the programme in the same spirit.

For FBA, the honest summary is the one its own community gives. Lewis, Nagarajan & Palsson (2012) survey the method family, O'Brien, Monk & Palsson (2015) survey what genome-scale models can predict, and Seif & Palsson (2021) write a whole Perspective on improving model quality and lifecycle, which is not a paper you write about a mature design tool.

17Where everyone went

Into domains where the cell does the work. And, decisively, into two technologies that succeed by not needing a model at all.

The diaspora is a matter of record: CAR-T and immune engineering, gut microbiome, rhizosphere and soil, bacterial cancer therapy, fermentation and metabolic engineering, antibiotic persistence. What the literature adds is that in each case the cell supplies most of the capability. Roybal et al. (2016) is combinatorial antigen sensing in T cells, where the T cell supplies essentially all of the capability and the engineered logic is an AND gate. Din et al. (2016) is synchronised bacterial lysis for in vivo delivery, where the payload is the point and the circuit is a quorum-triggered lysis timer.

And underneath the diaspora is the sharpest fact in this whole history.

The field's flagship case is worth following to the end, because all three schools' verdicts on it differ and the full texts settle which one is right.

Read the four together and the lesson is not about biology at all. The technical programme worked, spectacularly, by screening and iteration. What it did not do was change the economics, because the competing process is a plant. This matters in a specific way. The industry school's success criterion never required a predictive dynamical model either, and its failure mode was not a modelling failure. Both of the era's headline outcomes, the commercial ones and the circuit ones, are silent on whether a theory of composition would have helped. Only §18's curve speaks to that.

18It grew, but it did not scale

Twelve repressors and two activators in one cell, twenty years after three. That is a real gain and it is not scaling, and the field has been keeping score with exactly this metric since 2009.

The claim is that circuit engineering never scaled in the sense that electronics scaled. It is easy to get this wrong in an obvious way, by pointing at the rise from three regulators to fourteen and calling the claim refuted. That applies the wrong test. The claim is about a rate, not about whether any increase occurred, and rates can be measured. Two things make the measurement possible rather than rhetorical. First, there is an agreed metric: Purnick & Weiss (2009) defined circuit complexity as the number of regulatory regions in one designed system, and everyone since has kept score that way. Second, scaling has a definition: a fixed doubling period, sustained.

The rates are not close. Integrated circuits doubled every 1.7 years for sixty-four years, DNA sequencing every 1.4 years, chemical DNA synthesis every 3.1 years. Genetic circuits doubled every 7 to 9 years, depending on whether you anchor 2000 at the toggle switch or the repressilator, and the 2016-to-2020 interval is no faster at 8.2 years. Twenty years after its first artefact, the integrated circuit had 29,000 components on one die. Twenty years after its first artefact, synthetic biology had fourteen regulators in one cell.

Two features of that comparison do the real work. The gap is not a story about biology being slow: reading and writing DNA, the substrate the whole programme is built on, scaled at Moore-like rates over the same period. And the circuit curve does not merely sit low, it fails to steepen. A technology that is scaling gets faster as its tools improve. This one did not.

That is the claim, and the diagnosis, stated in a 2009 review from Ron Weiss's own lab, one of the three groups that built the founding circuits. It is not a retrospective judgement. The plateau was visible while it was happening, it was measured, and the explanation offered was that the design principles were too simple.

Within a year it was on Nature's news pages. Kwok (2010) reports that "although the number of published synthetic biological circuits has risen over the past few years, the complexity of those circuits, or the number of regulatory parts they use, has begun to flatten out", citing Purnick & Weiss directly. And the field kept using the same yardstick. Cello's own discussion measures itself against it:

Two doublings in eleven years, announced as an achievement, and correctly so. Nobody in the field claims a Moore's law for circuits. This section is not disputing the field's self-assessment. It is repeating it, with the arithmetic attached.

The 2020 result is the current ceiling. Shin, Zhang, Der, Nielsen & Voigt (2020) encoded a binary-coded-digit to seven-segment decoder in E. coli: seven strains, each carrying a circuit with up to 12 repressors and two activators, and 63 regulators and about 76,000 base pairs across all seven together. Per cell, the number is fourteen. The distinction matters, because a chip's transistor count is per die.

So the arc holds. What the 2020 paper adds is the reason, and the reason is what the rest of this essay is about.

And the model they replaced, stated in their own equation (1), is a Hill function with additive input composition:

They say so explicitly: "The first model for NOR gates simply treated the input as the sum of the RNAP fluxes of the upstream promoters." That is Hill plus additivity, cited to Kelly et al. 2009 and Nielsen et al. 2016. Going from three regulators to fourteen required abandoning additivity and adding a resource-utilisation term, which is RNAP flux accounting. Those are precisely the two assumptions §19 identifies as one violated inequality.

19Retroactivity and burden are one inequality

Both surprises say the same thing: a pool assumed to be in excess was not in excess.

Here is the central technical claim of this essay. Line up the two headline failures of the engineering programme and ask what each one is, mechanically.

Retroactivity. A transcription factor drives a downstream promoter. To do so it binds the operator. Bound molecules are removed from the free pool. So the effective input to the downstream gene, and the effective level of the upstream signal, both depend on how many downstream sites there are. The assumption that broke is the complex is a negligible fraction of the total transcription factor.

Growth burden and resource competition. A circuit's mRNAs compete with the host's mRNAs for ribosomes, and its genes compete for RNA polymerase. Bound machinery is removed from the free pool. So the expression of each gene depends on how much every other gene is demanding. The assumption that broke is the complex is a negligible fraction of the total ribosome or polymerase pool.

These are not two phenomena. They are one violated inequality, applied to two different shared species. And crucially, it is the same inequality that licenses writing a Hill or Michaelis–Menten function in the first place.

20The inequality, stated properly

It is not "substrate greatly exceeds enzyme". The correct condition is a ratio involving the affinity, and the difference is exactly where gene circuits live.

Stated loosely, the condition is S_tot ≫ C, so that S_tot ≈ S. That is the right condition. It is worth having the classical sharpened form as well, because the naive version ("enzyme is much less abundant than substrate") is what most people carry around and it is not the criterion.

For the standard scheme E + S ⇌ C → E + P with initial totals E₀ and S₀, the quasi-steady-state approximation, and therefore the Michaelis–Menten rate law, is valid when

Segel & Slemrod (1989, SIAM Review) derive this as the necessary condition, and note that it is strictly stronger than the timescale-separation condition alone. It reduces to E₀ ≪ S₀ only when the substrate is well above the affinity. When affinity is tight, K_M is small and the criterion becomes harder, not easier.

And here is the review that states the modern consequence in exactly these terms:

Read the list of false predictions against the founding papers of §9. Ultrasensitivity, bistability, oscillations. The toggle switch is a bistability claim resting on a cooperativity exponent. The repressilator is an oscillation claim resting on a Hill coefficient. Neither paper is wrong about what it built, because both were verified experimentally. The point is narrower and more damaging: the model class used to reason about them cannot be trusted to get those three features right, which is why the field could not predict its way from three genes to fourteen.

One number from §9 makes this concrete. The repressilator's reported K_M is 40 monomers per cell. A handful of plasmid copies each carrying operator sites puts the site count within an order of magnitude of that. So ε = t_sites/(K_D + t_TF) is not small. The founding model of the field was applied, in its own parameters, at the edge of its own validity.

21Why this is a missing model class, not a missing parameter

A parameter error shrinks when you measure better. This one does not, because the object being measured does not exist independently of its context.

The diagnosis is that the field lacked a foundational theory of the right kind. Not a law like Newton's, but a characterisation of a model class guaranteed to contain every biological system. This is the part of the case that is an argument rather than a fact, so it deserves the sharpest statement and the strongest available objection.

The argument. Mechanical engineering has the Lagrangian. Every mechanical system you might build is in that class, so system identification is a search inside a family you know contains the answer. Circuit theory has Kirchhoff plus constitutive relations, with the same guarantee. Given such a class, theory and experiment can close a loop: the model proposes, the experiment disposes, and the discrepancy is informative because it must be a discrepancy within the class. That loop is what drove the electrical and mechanical revolutions.

Biology's analogue exists in principle, and that is the pivot. By the universality of biochemistry, the class of all chemical reaction networks certainly contains every cell. Everything mechanical, electrical, thermal or osmotic that interacts with life interacts through that core. So a guaranteed class is available. It was simply not used, because in 2000 it was neither writable nor simulable at scale, and Hill and Michaelis–Menten were.

The consequence is that the field's working class was smaller than biology. Not approximate in a controlled way. Smaller. Real systems sat outside it, and the standard symptoms of that condition are exactly what §13 through §16 document: models that fit in isolation and fail on composition, parameter estimates that shift when context changes, and predicted dynamical features that do not survive.

22Four answers on offer

The field did respond to the missing class. It produced four distinct strategies, and they are still competing.

It is worth being explicit that the diagnosis in §21 is not a complaint that nobody noticed. Everyone noticed. Four coherent responses exist, each with a real success record and a real cost.

23Binding and catalysis

A cell cannot change pressure, temperature or pH at will. It can only change whether a catalyst is present. That single restriction is what turns all-of-chemistry into a workable class.

This section states the proposal compactly. The full development is the companion essay, The Biomachine Perspective.

Start from the restriction. A chemist gets to change conditions: heat the flask, change the solvent, swing the pH. A cell does not. Its interior is held within narrow bounds, which is most of what homeostasis is for. So a cell cannot make a reaction go by changing conditions. Its only lever is whether the enzyme for that reaction is present and active. Therefore every load-bearing reaction in a cell is an enzymatic reaction, and every enzymatic reaction has the same two-part structure: molecules bind to form a complex, and the complex is catalysed into products.

Three properties make this a candidate rather than just a rewriting.

It contains the systems it needs to. Binding networks are universal in the relevant sense: they can approximate any positive continuous function arbitrarily well. So restricting from all chemistry to binding-plus-catalysis loses no expressive power over the regulatory functions a cell can implement.

Its architecture is fixed and knowable. The catalysis matrix S is what genome annotation and metabolic databases already give you. That is the structural information the genome supplies for free, in Bailey's sense. What is unknown is the binding network L, and that is where the learning problem lives.

The unknown part is at equilibrium, which makes it tractable. Binding is fast, so the binding layer is an equilibrium problem, not a stiff dynamical one. This is the same structural gift that made equilibrium statistical-mechanics models the starting point for machine learning, and it means gradients through the binding layer are well behaved. Mechanism identification then reduces to sparsity in the binding affinities: an affinity of zero means that complex does not form.

24The missing shock

Each previous wave needed an enabling event. The honest answer to "what is the third one" is that we do not yet know, and there are three candidates with different implications.

One structural point in the history above is worth naming. Theory alone has never started one of these waves. Each time, a discovery arrived that made a new object visible, and the three schools moved because they could suddenly see the same thing. So the question is not only whether the model class is right. It is what the enabling event will be.

Candidate one: omics at scale. The 1970s gave named mechanisms. The 2000s gave a parts list. Large-scale multi-omics and perturbation data give, for the first time, the parametric half of Bailey's split, at scale and across conditions. If the binding network is what has to be learned, this is the data it would be learned from.

Candidate two: learned model classes. This candidate deserves the most care, because Figure 6 already contains its precedent. Protein structure prediction crossed the frontier that gene circuits did not. It did so with a learned model class, trained on a large curated dataset, rather than a derived one. AlphaFold and then generative design did for one biological question exactly what is argued here to be missing for another. That is encouraging for the ambition and awkward for the method, because it suggests the class need not be derived from first principles at all.

Candidate three: a mechanistic model class that is also learnable. This is the bet behind the foundational virtual-cell programme, and it is an attempt to take both lessons at once. Keep the class mechanistic, so that its interior is interpretable and its discrepancies are informative. Make it learnable at scale, by using the equilibrium structure of the binding layer to get well-behaved gradients. The claim being tested is that binding and catalysis is the class where those two demands are compatible.

25What the record shows, and what it does not

Three findings in this history are solid enough to argue from. The proposal built on them is not yet, and it should be held to a specific deliverable.

The arc has been: three questions, three moments when a discovery let all three be asked of one object, and a third moment that produced less than the first two. Part V's answer is that a single modelling assumption failed and was never replaced. That answer is an argument, so it is worth separating what the record establishes from what the argument adds to it.

Those three are why the history is worth telling as a history rather than as an opinion. Each one is a number or a sentence from a paper by someone who was building at the time, not a retrospective judgement imposed on them.

What to distrust here

Three places where the evidence is thinner than the prose around it, stated so a reader can discount them appropriately.

• Figure 7's circuit series is a lower bound, not a census. It tracks the largest single-cell dynamical circuit I could source. A larger one published since 2020 would move the last point, though a per-cell count would have to roughly double to change the conclusion about the slope. The comparison series, transistor counts and instrument read lengths and synthesis milestones, are public engineering records rather than papers, and the caption says so.
• Figure 6 is an argument, not a measurement. Both axes are qualitative and the placements are the claim of §17 rather than data. It earns its place by making the pattern legible, not by establishing it.
• The four strategies of §22 are not mutually exclusive, and the fourth is the least proven. Patching rate laws, finding phenomenological laws and screening are all in production use with track records. Changing the model class has a thesis, a preprint and a programme. Comparing them as equals overstates the fourth.

The calculation that would settle it

What is missing from the case for §23 is not a paper. It is a calculation: a worked demonstration that the binding-and-catalysis class predicts a composition failure a Hill-function model gets wrong, on a circuit someone has already built and measured. Retroactivity and burden are both available as test cases, because both are documented failures with published numbers, and both are supposed to fall out of L x = q rather than being fitted.

Until that exists, Parts V and VI are a diagnosis with a proposed treatment and no trial. The three deliverables named at the end of §24 are the terms on which the treatment should be judged: extrapolate to a design no library contains, transfer a mechanism from one context to another, or state in advance that a proposed behaviour is unreachable. Nothing in the history above obliges anyone to believe those are achievable. It only shows why they are the right things to ask for.

References

Every one of the 107 entries below was read in full. PDF marks a verified full text. TXT marks one obtained as complete text rather than PDF, from the PMC open-data archive. Ordered by the section that first uses them.

Companion essay: The Biomachine Perspective develops the reaction-order and dominance theory referenced in §23.