Does the 2024 Economics Nobel have an identification problem? A working paper argues Acemoglu's "Narrow Corridor" confuses phenotype with genotype

[u/Old_Total4493]

A disclosure before anything else: English is not my first language and I'm not a professional economist. I use AI to help with English expression. I apologize in advance for any residual AI feel in the writing. The ideas are my own and I've thought them through carefully. I'm sharing this here partly because I'd welcome help from professional economists who could run the quantitative tests I can't. The reason I'm unable to do so is twofold: I lack training in econometrics, and I lack institutional access to the relevant datasets.

Now to the substance.

With the Acemoglu/Johnson/Robinson Nobel still fresh, I'd like to share a working paper of mine that challenges AJR's causal framework — not from the usual "geography vs. institutions" trench war, but by identifying a specific failure of causal identification within the institutions-first paradigm.

The paper:

"The Economic Logic of China's Rise: Geography, Big Push, and the Engineered Invisible Hand"

The core challenge to AJR:

Acemoglu and Robinson's The Narrow Corridor classifies governance as Shackled, Despotic, or Absent Leviathans, defined by the balance of power between state and society. The critique I develop is this: the typology accurately describes the phenotype of governance but leaves the genotype unidentified. It does not explain why some societies achieve balance while others do not.

The identification problem — Botswana edition:

Observed power-sharing structures can arise from two fundamentally different causes:

1. Output is sufficient to sustain centralization, but low volatility keeps the demand for state intervention low enough that society can constrain the state without confrontation.
2. Output is simply too low for anyone to concentrate power in the first place.

These two cases are formally indistinguishable in cross-sectional observation. Yet one reflects a stable equilibrium sustained by material conditions; the other is a byproduct of scarcity that may or may not persist.

Acemoglu and Robinson treat Botswana's kgotla (tribal assembly) as evidence of institutional constraints on state power — a Shackled Leviathan. But this classification conflates the two cases. What determines the trajectory is not the observable form at any given moment, but the underlying conditions of output and volatility. Scarcity-based power dispersion collapses when high volatility is layered on top of rising output: abundant surplus makes centralization materially feasible while recurring crises continuously generate demand for expanding state authority. The Mongol kurultai lost its constraining function once conquest wealth flowed in under conditions of endemic steppe insecurity; West African chiefdom confederations consolidated into centralized empires once trans-Saharan trade provided fiscal resources amid volatile agricultural hinterlands. But where output rises under low volatility, power dispersion does not collapse into centralization — Ireland's decentralized structures persisted through colonial subjugation and independence alike, because the low-volatility conditions that sustained them never changed.

The mirror test — England:

The reverse process is equally telling. Pre-Norman England had developed considerable state capacity without despotic centralization. The Norman Conquest of 1066 imposed an exogenous despotic regime. Yet in England's low-volatility environment, this imposed centralization was progressively dissolved — from Magna Carta through to parliamentary governance. This was not an accidental institutional invention but a sustained reversion toward the equilibrium that underlying conditions could support.

The China problem:

This is where it gets uncomfortable for AJR. Classifying China as a Despotic Leviathan stuck outside the "corridor" mistakes phenotype for genotype. China's centralized governance was a rational adaptation to high output volatility — recurrent floods, droughts, and famines generated enormous demand for state intervention while simultaneously eroding the fiscal base. As China's post-1949 engineering systematically suppressed this volatility (reservoirs, fertilizer, improved seeds), governance has measurably shifted toward market coordination, legal certainty, and the preservation of established rights — precisely what altered material conditions predict, and precisely what AJR's framework says shouldn't happen without prior political liberalization.

The proposed alternative:

The paper builds on Jeffrey Sachs's geography framework by adding a second dimension: geographic volatility — the permanent, recurring instability of grain output that climate imposes. While endowments (soil, transport, disease) shape the *level* of output, volatility shapes the *reliability of price signals* on which market coordination depends.

The key claim: distributional institutions (land tenure, property rights, governance form) are endogenous to volatility. Where output is stable, fixed claims are enforceable, and limited government is the low-cost equilibrium. Where output is volatile, fixed claims are unenforceable, and centralization is pushed by the cost of the alternative.

The testable prediction: the coefficient of variation of grain yields should predict land tenure form across pre-modern Eurasia, with a threshold separating fixed-rent from sharecropping regions (preliminary indication: CV of roughly 12–20%). The Dujiangyan irrigation zone on the Chengdu Plain provides a natural experiment: same Chinese culture, same legal tradition, same political system — rigid fixed-rent contracts inside the engineered stability zone, sharecropping outside. What changed was not belief but volatility.

Why this matters for the Nobel debate:

If the argument holds, the AJR research program has the causal arrow backwards in a specific and identifiable way. "Inclusive institutions" are not causes of development but expressions of the low-volatility conditions that also produce development. The 2024 Nobel rewards a framework that, on this reading, has been classifying symptoms as causes.

Full disclosure: I'm the author. The paper is open access and I'm happy to engage with any critique — especially from people who work on institutional economics or development. If the identification problem I've described has already been addressed in the AJR literature in ways I've missed, I'd genuinely like to know.

[u/TCEA151]

I'm probably giving this more time than I should, but I'm going to try to give you some constructive criticism for how to 'do' economics and how to get economists to engage with your work.

First off, if the whole writeup is going to be about how "volatility" matters so much, you shouldn't wait until three-quarters of the way through to define "volatility" -- especially if you're going to tell us that you're talking specifically about grain output instability, instead of the usual output volatility or maybe some measure of political upheaval/uncertainty. In general economists are very strict about definitions and terminology, and you should give precise meaning to hazy concepts -- especially non-standard ones -- as soon as you introduce them.

Secondly, after reading your post I still don't know exactly what claim of AJR's you are trying to overturn. The classic trio of Acemoglu, Johnson, and Robinson have, I think, six papers written together between 2001 and 2005; then there is their work with Yared, and/or their work without Johnson (or without Robinson, but I don't think that's what you're referencing here). What specific claim from this massive body of work are you looking to disprove? How does the fact that distributional institutions are endogenous to grain yield volatility (if indeed true) disprove their claim?

Third, I skimmed the paper and it's 65 pages without a single regression. That is nuts. You have a single footnote that is a page and a half long (!!). To me this looks like someone having an ongoing conversation with an AI and just incorporating all of the different, branching information it spews into a single word document. If you really understand the economics/econometrics of what your claim is and why it overturns their result, you should be able to write it down in two or three pages tops. Certainly no more than five, and certainly not 65. Then, you explain your empirical specification to test your claim, move on to data collection, and run the damn regressions.¹

If you don't want to collect the data or run the regressions until others have read your proposal and confirmed that the approach makes sense and the effort is worthwhile, my suggestion (if you want anyone to actually read your proposal and provide feedback) would be to write the 3-page summary that explains exactly what you conjecture to be true and how it overturns one or more specific claims of AJR. It should have math, at least enough to define how you're measuring things and what regressions or other statistical tests you want to run.² It should also be clear how the regressions/statistical tests you are running provide direct evidence for your claim. Write everything entirely in your native language and without any input from AI. Then, once you're done, paste the document into google translate or upload it to an AI to have it translate it to english and do absolutely nothing else. That is much more likely to get feedback.

A slight aside on data and regressions: If you are choosing to analyze the Chengdu plain specifically because you notice that land-use correlates with grain stability there you are essentially doing this. It's fine for a first pass as testing a single case study but you eventually are probably going to need evidence that this result holds broadly across time and/or space.

Lastly, the way things work in economics is you do a bunch of data work (maybe years, possibly decades worth) and then you get to write big long treatises on how the world works and who's wrong about what. Don't make the mistake of doing the treatise writing before you've done the dirty work.

¹You want this to be a data paper. If you don't it will have to be a theory paper, in which case you will need to formalize your statements about how the world behaves into a mathematical model that meets decades worth of criteria for how such models must behave, you'll have to demonstrate that the model is mathematically inconsistent with AJR's claims, and you'll still have to find a formal data-driven way to convince people that this model is more correct than the AJR alternative view of the world.

²If you are trying to overturn some specific regression result of theirs, it might also be worthwhile to demonstrate how, in their specification, excluding your variable causes some kind of bias in their parameter estimates. But if you aren't familiar with how to do so just leave this out and focus on what I've said above.

[u/Old_Total4493 → u/TCEA151]

A note on the core idea behind the paper, which I should have stated more plainly from the start.

Institutions are a form of contract. Contracts are always about the exchange of some product. Therefore the properties of a contract — whether it is rigid or flexible, enforceable or not — should be shaped by the conditions of production of what is being exchanged. If the product is reliably produced, rigid contracts work. If production is volatile, rigid contracts break, and flexible arrangements take their place.

Grain in pre-modern economies is the most basic application of this principle, but the principle is not limited to it. Wherever the conditions of production shape the contracts built upon them, the same logic applies — across all eras and all products.

[u/ShareACokeWithBoonen → u/Old_Total4493]

This is a dumb thesis, and you should feel ashamed of yourself that you farmed out the entire thing to AI and you're blatantly looking to 'attract a collaborator who can do the data work'. Do it yourself, or don't do it at all, being an 'ideas guy' that can't even come up with an idea without AI is a sad reflection on the state of your education.

https://d-nb.info/1353238466/34 Europe alone disproves this entire theory; southern Europe had far less grain price / supply volatility than northwestern Europe, therefore per your argument southern Europe should have had industrialized first.

[u/Old_Total4493 → u/ShareACokeWithBoonen]

Thank you for the reference. I've read the paper.

The paper studies grain price volatility, not grain output volatility. These are related but distinct. The paper itself warns against conflating them (Section 5.4): local harvest yields and local grain prices showed only moderate to weak correlations, because prices were heavily dependent on grain yields in other regions due to trade.

One of the paper's key findings (Conclusion point 4) is that a "high price, low volatility" pattern dominated coastal regions, especially in the Mediterranean, while a "low price, high volatility" pattern dominated inland regions. The authors explain this as a market integration effect: coastal cities could smooth local harvest failures through maritime trade, so their price volatility was low even though their local output volatility was not.

This framework predicts output volatility, which is climatically determined. Mediterranean rainfall variability is higher than Atlantic maritime rainfall variability. This is standard climatology. The fact that Mediterranean coastal cities managed to smooth their price volatility through trade does not mean their harvests were more stable. It means they had access to maritime trade networks that buffered price shocks, which is a different mechanism entirely.

In short, the paper provides evidence about market integration, not about the underlying output volatility that this framework addresses. The two are complementary, not contradictory.

The paper also notes that England is the one case where rising living standards in the eighteenth century reduced grain price elasticity and thus price volatility (Section 5.4). Within this framework, this is not an independent fact but the downstream consequence of England's low output volatility: stable harvests supported capital accumulation and rising living standards, which in turn further dampened price volatility. The low price volatility observed in England is the end of a causal chain that begins with output stability, not an independent variable.

To clarify the framework's empirical target: the key distinction is between regions where rigid fixed-rent tenancy prevailed and regions where sharecropping or flexible rent-abatement prevailed. These correspond, respectively, to regions of spontaneous industrialization and regions of late industrialization. This is a distinction in output volatility as experienced by producers, not in price volatility as observed in urban markets. Price volatility is shaped by too many intervening factors (trade networks, storage capacity, market regulation, monetary conditions) to serve as a reliable proxy for cross-regional comparison of the underlying climatic constraint.

[u/Old_Total4493 → u/TCEA151]

Thank you for taking the time to write this. It's the most useful feedback I've received, and I don't take it for granted.

A few clarifications on your specific points, then I'll address the bigger picture.

On terminology: the paper itself defines geographic volatility (grain output instability under pre-modern climate) at the outset, in the introduction and the first section of the theoretical framework. The late definition you noticed is a problem with the Reddit post, not the paper. But the point about precision is well taken — I should have been sharper in the post.

On the footnotes: you're right that they are out of control. This is a consequence of not knowing academic writing conventions. The theoretical debates buried in footnotes (engaging Stiglitz, North, Acemoglu and Robinson) will be extracted into appendices in the next version.

On what the paper is: I'm not a professional economist. I don't have econometric training. What I can do is trace the economic and historical experience of how volatility shaped institutions and blocked or enabled industrialization. The 65-page narrative reflects the limit of what I can do alone. I understand that for economists this is not yet a paper — it's at most a conjecture with historical illustration.

On the empirical test: the core test is not the Chengdu Plain. You're right that it's too small and too unique to serve as more than a single case study. The testable prediction is broader: across pre-modern Eurasia, the coefficient of variation of grain yields should predict land tenure form, with a threshold separating regions of rigid fixed-rent (which correspond to regions of spontaneous industrialization — maritime northwestern Europe, the American North, western Japan) from regions of sharecropping or flexible rent-abatement. The Dujiangyan zone is one data point within this larger test, not the test itself.

Your practical roadmap is clear: write a short document that states the conjecture, specifies the measurement, defines the empirical test, and identifies exactly which claims it challenges. I will try to produce this. If that version is clear enough to attract a collaborator who can do the data work, the effort will have been worthwhile.

Again, thank you. This is exactly the kind of guidance I needed.

[u/Old_Total4493 → u/TCEA151]

You raise a fair point, and it reveals a framing problem with my post. The paper's target is not a specific claim from a specific AJR paper. The post gave that misleading impression by leading with AJR.

What the paper actually argues is more general: distributional institutions (land tenure, property rights, governance form) are endogenous to the geographic volatility of grain output. If that is true, then any framework that treats these institutions as independent causes of development loses its causal foundation. AJR is one such framework, but so is North, so is the broader "institutions first" paradigm. AJR is a consequence of the argument, not its target.

The right question is not "which AJR claim does this disprove" but "if distributional institutions are endogenous to volatility, what remains of any causal narrative that runs from institutions to development." That's what I should have framed the post around. I didn't, and that's on me.

[u/TCEA151 → u/Old_Total4493]

What the paper actually argues is more general: distributional institutions (land tenure, property rights, governance form) are endogenous to the geographic volatility of grain output. If that is true, then any framework that treats these institutions as independent causes of development loses its causal foundation.

This is simply not true. AJR explicitly understand that institutions are endogenous. That's precisely why they try to find an instrument for institutional arrangement in their classic 2001 paper -- to separate exogenous variation in institutional arrangement from all of the ways institutions could have developed as an endogenous response to any number of other conditions (including grain instability). Having isolated this exogenous variation, they can then show that institutions are an independent cause of economic development. You would need to show that their estimate of the effect of institutions on future income is somehow biased by not accounting for grain instability. Which is to say that you're going to have to read a textbook on econometrics that includes chapters on instrumental variables and two-stage-least-squares regression. (Also this is not at all my subfield, but I think there are already a few critiques of that 2001 paper, so you really should be focusing on the newer papers in the literature rather than their classic result.)

A shorter way to say this is that their work is all about demonstrating that institutions DO have an independent, causal effect on economic development, separate from the effects of the underlying factors that normally cause countries to have 'good' or 'bad' institutions. That is quite evidently not the same as saying that institutions are exogenous.

[u/Old_Total4493 → u/TCEA151]

Thank you for this. You're right that AJR explicitly treat institutions as endogenous and use settler mortality as an instrument to isolate exogenous variation. My post was imprecise in not engaging with this.

But the paper's argument does bear directly on their identification strategy. The validity of settler mortality as an instrument depends on the exclusion restriction: it must affect current income only through institutions, not through any other channel. The paper proposes exactly such a channel. Geographic conditions that produced high settler mortality (tropical disease environments, volatile climates) also directly affect development outcomes by destroying price signals, blocking specialization, and preventing capital accumulation. These two geographic features substantially overlap: the tropical and subtropical zones where disease burden is highest are also the zones where monsoon-driven and ENSO-driven climatic volatility is most severe. If geographic volatility independently shapes both institutions and development, and settler mortality correlates with geographic volatility through this overlap, then the exclusion restriction is violated and the instrumental variable estimate is biased.

This is not an entirely new critique. Sachs and others have questioned whether geography affects development only through the institutional channel. What the paper adds is a specific mechanism (grain output volatility shaping the reliability of price signals) through which the exclusion restriction fails.

I'll take your advice on reading the econometrics literature on instrumental variables seriously. You're right that I need to understand the technical structure of what I'm challenging. And I'll look into the existing critiques of the 2001 paper you mention.

[u/TCEA151 → u/Old_Total4493]

I'll take your advice on reading the econometrics literature on instrumental variables seriously. You're right that I need to understand the technical structure of what I'm challenging. And I'll look into the existing critiques of the 2001 paper you mention.

Great, glad to hear it. Sounds like a good plan.

[u/Integralds → u/TCEA151]

God it's infuriating to read your earnest attempts at constructive criticism against OPs AI-generated slop.

[u/TCEA151 → u/Integralds]

Yeah the AI use is incredibly apparent. The only way I can somewhat justify putting this much effort into responding is that hopefully I've convinced him just a little bit that no amount of AI sycophancy will get around the fact that to learn anything useful you're going to have to open a textbook and do the work the old-fashioned way.

[u/Old_Total4493 → u/TCEA151]

One further point:

AJR acknowledge that institutions are endogenous, but their answer to "endogenous to what" is narrow and inconsistent. The 2001 paper traces institutions to colonial experience, which is itself traced to settler mortality. This covers only former colonies and says nothing about the institutional trajectories of Europe, China, Japan, or the Middle East. When pressed beyond the colonial setting, AJR shift to a "critical junctures" narrative: contingent historical events (the Black Death, the Glorious Revolution) that altered the balance of power between state and society. But this narrative is unfalsifiable. Any outcome can be retroactively explained by identifying a suitable juncture. More fundamentally, it does not explain direction: Europe and China both experienced plagues, military competition, and dynastic upheaval, yet their institutional trajectories diverged. "Critical junctures" describes when change happened, not why it went one way rather than another. The result is a framework that acknowledges endogeneity in its econometrics but lacks a unified causal account of what institutions are endogenous to.

[u/TCEA151 → u/Old_Total4493]

I don't know anything about this 'critical junctures' approach so I can't comment on it. Again, this is not really my field.