Regional economics

More service jobs, less technical AI use — a subnational look

Anthropic's Economic Index paired with OECD regional employment statistics, across 279 regions in 35 countries. The regions you would most expect to be doing technical work with AI are — within their own countries — the regions doing proportionally less of it.

Carlos Ignacio Navarro · August 2026 · 5 min read · appendices ~15 min more

Most of what people ask Claude to do is professional work, and that is true almost everywhere. Across 279 regions in 35 countries, the professional and managerial occupations — management, business, computing, engineering, law, education, health — account for about three-quarters of usage. How service-heavy a region's economy is tells you essentially nothing about that share.

Narrow the question and the picture changes. The Economic Index sorts each conversation into one of the 22 major occupational groups of the US Standard Occupational Classification, and one of those groups is Computer and Mathematical — software development, systems analysis, data science, statistics, actuarial work. That is the group this piece is about, and I will call it technical usage from here on. It averages 24% of a region's usage and runs from about 19% to 32%.

The obvious guess is that technical usage concentrates where the offices are: financial districts, professional-services hubs, the regions where employment sits in offices rather than on factory floors. It is a reasonable guess. In the data it is backwards.

Pairing the Economic Index with the OECD's regional statistics, I compared 279 regions across 35 countries — states, provinces, Länder and their equivalents, the first administrative tier below the national government. Within countries, regions with more service employment show a lower technical share of usage. Moving from the 10th to the 90th percentile of regional service employment — from 57% of employment to 86% — is associated with a drop of about 1.7 percentage points in the technical share, roughly 7% of its average and about 1.3 standard deviations of the variation that exists inside a typical country.

That is not a rounding error, and it is not driven by any one country.

Three ways to measure AI, and a gap between them

There are broadly three ways economists have measured artificial intelligence in the economy, and they answer different questions.

The first is exposure: what AI could plausibly do. Felten, Raj and Seamans built the standard measure here, linking catalogued applications of AI to the workplace abilities that O*NET uses to describe occupations, then aggregating to occupations, industries and geographies. Their measure is deliberately agnostic about consequences — it says nothing about whether AI replaces a worker or makes them faster. It measures potential contact, not outcome.

The second is adoption: what workers and firms say they do. Bick, Blandin, Deming, Fuchs-Schündeln and Jessen fielded harmonized surveys across the US and Europe and found a substantial adoption gap, with US workers reporting higher use than their European counterparts. The more interesting result is what explains it. Differences in who works where — occupation, industry, firm size, demographics — account for a good share of the gap, and once you add whether a worker's employer actively encourages AI use, very little of it is left unexplained. Adoption looks less like a story about national character and more like a story about workplaces.

The third is usage: what people actually do, observed rather than reported. This is what the Anthropic Economic Index provides, by classifying the content of conversations with Claude. Scott Davis at the Dallas Fed recently connected two of these traditions, showing that the link between a sector's AI exposure and its recent productivity growth is stronger in countries where AI usage is more intense.

It is a genuinely useful result, carefully framed as correlational, and it is where this piece starts. A country-level comparison has about twenty observations, and countries differ in a thousand ways at once — language, regulation, income, industrial structure, broadband. The pattern is visible at that scale; what sits behind it is not separable there.

On Davis's own usage index, Germany sits at 1.79 and France at 2.66 — a gap of nearly 50% between two neighbouring economies of similar size and wealth. "Country" turns out to be a coarse unit even for the thing being measured. Whatever is driving AI usage, it is not operating at the level of continents.

That is the gap this piece walks into. Release 6 of the Economic Index reports usage for 652 first-level administrative regions rather than just countries. That is enough to stop comparing countries to each other and start comparing regions inside the same country — provided you can find comparable economic statistics for each region, which is where the OECD comes in and where most of the sample goes. This piece covers 35 countries rather than the 128 the Economic Index reaches because comparing regions means knowing each region's employment structure, and the OECD Regional Database is the only harmonized source for that. The full accounting from 652 regions down to 279 is in Appendix A.

Why comparing regions inside countries matters

Comparing Estonia's AI usage to Poland's tells you something, but you can't say what. The two differ in income, language, regulation, industry mix and digital infrastructure, and any of those could drive the result.

Comparing Bavaria to Saxony-Anhalt is a different exercise. Both sit under the same national government, the same language, the same regulatory regime, the same broadly similar institutions. What differs is regional: the local economy, the local labour force, the local mix of employers.

A word on what I mean by service employment, because it is broader than it sounds. It is the standard national-accounts definition: everything that isn't agriculture, mining, manufacturing, utilities or construction. Retail and wholesale trade, transport, hotels and restaurants, information and communication, finance, real estate, professional and administrative services, public administration, education, health, arts and recreation. A supermarket cashier, a bus driver, a nurse and an investment banker are all service employment. It is not a synonym for office work or white-collar work — and it is not the same thing as the white-collar share of usage from the opening, which describes what people ask Claude to do rather than where they work. Regions in the sample run from about 37% service employment to 97.5%.

That breadth is worth worrying about: a region can be service-heavy because of its hotels or because of its law firms, and those are not the same economy. So I tested a narrower measure covering only information, finance and professional services. It gives the same sign, which means the finding is not manufactured by lumping restaurant work in with professional services. It also cannot be separated from how much Claude usage a region generates, which is why the broad measure is the one I report. Appendix A has both.

Statistically this is a country fixed effect, and it does the heavy lifting throughout. Every comparison below is between regions of the same country. National differences are subtracted out before anything is estimated, so nothing here can be explained by a country being rich, or English-speaking, or lightly regulated.

Map and scatter plot showing the technical share of Claude usage across 279 regions, with a downward-sloping relationship against service employment. — Figure 1 — Technical share of Claude usage across 279 regions

The finding

Across all 279 regions pooled together, service employment and technical AI use are negatively correlated at −0.65. That much could be a composition effect: rich service-heavy countries might simply differ from poorer industrial ones.

It survives the country fixed effect. Within countries, a one percentage point increase in a region's service employment share is associated with a 0.058 percentage point decrease in the technical share of usage. Adding controls for regional GDP per capita and the share of the population with tertiary education attenuates the estimate but does not break it.

Figure 2 — Within-country scatter, with a country selector

How to read this. Both axes are differences from a region's own country average. A region sitting at zero on the horizontal axis has exactly the service employment share that is typical of its country — not of the world.

Pick a country from the dropdown and its regions stay in colour while the rest fade to grey. That re-centring is what a fixed effect does: inside Germany the comparison becomes Bavaria against Saxony-Anhalt, and Germany's national position drops out of the arithmetic entirely. The dotted line is that country's own slope, drawn for the eighteen countries with at least five regions.

Sixteen of those eighteen slope the same way as the pooled estimate. The two that don't — Chile and Poland — are weak enough to be indistinguishable from noise at six and eleven regions. I come back to that below.

The United States is the cleanest test available. It contributes 51 regions measured on a single consistent statistical system, so nothing hinges on harmonizing definitions across borders. Within the US, the relationship is more than twice as strong as the international average.

Figure 3 — US states: service employment against technical usage

One further piece of the pattern is worth stating, because it narrows what can be going on. When the technical share of usage falls, no particular occupation absorbs it. Four occupational groups — office and administrative support, sales, education, and arts and media — are reported in every single region, so nothing is missing from that comparison. Their share of non-technical usage is essentially constant from region to region. When the technical slice shrinks, everything else expands in proportion. Nobody picks up the slack.

The same holds one level up. Recall that professional and managerial work is about three-quarters of usage everywhere and shows no relationship to service employment. Technical work sits inside that block, and it does fall — so in principle the rest of the block should be rising to compensate. It shows no detectable rise: +0.03 with a t-statistic of 0.99, and nearer zero still once regional usage volume is controlled for. Management, business, legal, health and education usage are not visibly absorbing what computing gives up.

How hard I tried to break it

A surprising result deserves more scepticism than a confirming one, so this is where I spent most of the time.

No single country drives it. I re-estimated the model 35 times, each time dropping one country entirely. The coefficient ranged from −0.052 to −0.067 across all 35 refits, and the median landed exactly on the full-sample estimate. Not one refit came close to zero.

Figure 4 — Leave-one-country-out: 35 refits

It isn't a US result in disguise. The US is 18% of the sample, which is a lot of weight for one country. Dropping it entirely leaves the estimate at 90% of its original size and still comfortably significant.

It isn't one strange region. Washington DC is an extreme outlier, with 97.5% of employment in services. Removing it changes nothing. More tellingly, when I identified the five regions with the most statistical leverage over the coefficient and dropped them, the relationship got stronger. The influential observations were working against the result, not creating it.

The standard errors aren't flattering me. With 35 countries, one contributing a fifth of the observations, conventional clustered standard errors are optimistic. I re-ran the key test with a bootstrap that resamples at the country level rather than trusting an asymptotic approximation. The honest critical values are wider than the textbook ones, and the result clears them anyway.

A completely separate measure of technical usage agrees. The Economic Index classifies each conversation two ways: by the occupation the task belongs to, and by the artifact it produced — the concrete thing the user ended up with. Everything above uses the occupational classification. So I built a second measure from the artifact side, adding up the shares of usage that produce code fixes, scripts, database queries and configuration files.

Nothing about how it is built is shared with the first. Different classification scheme, different question, and — this is the part that matters — no suppression at all. The artifact data is reported for all 652 regions with every category present, so none of the disclosure problems described in the appendices apply to it. No coverage variable, no renormalization, no volume control needed.

It gives the same answer. Within countries, a one point rise in service employment is associated with a 0.056 point fall in the artifact measure, against 0.058 for the occupational one. Measured in standard deviations, the artifact version is slightly stronger. The two correlate at 0.65 within country — closely enough to be tracking the same thing, loosely enough that their agreement isn't circular.

Figure 5 — The two measures side by side

One caveat worth stating: these are two classifications of the same conversations, not two independent datasets. The test rules out quirks of the occupational taxonomy and of the disclosure structure, which is what was in doubt. It cannot rule out something common to the underlying sample.

And I rebuilt the whole thing in another language. I replicated the entire pipeline in Stata — the data extraction, the merge, the estimation — working only from my own written method description rather than from the original Python code. That constraint is the point: porting code line by line reproduces whatever misunderstanding was baked into it, while rebuilding from the description tests whether the description is actually right. Every intermediate dataset and every published estimate came back to floating-point tolerance. It surfaced three reporting issues, all documented in the appendices, and no substantive error.

The relationship also holds at a finer geographic grain, and in a specification that drops the education control. Details are in the appendix.

The explanation I couldn't confirm

I had a tidy story for why the sign comes out this way, and I want to be clear that I could not confirm it.

The story is breadth. In an industrial region, the small population of Claude users skews heavily toward engineers and IT staff, so the technical slice looks large. As service employment rises, usage spreads across sales, administration, healthcare, education and management, and the technical slice shrinks by dilution rather than by any decline in technical work.

That is a testable claim, not an interpretation, so I tested it — three different ways, and all three failed. The obstacle is a privacy feature of the data: the Economic Index withholds occupation categories in a region when the underlying counts are too small, so a region with more usage overall has more categories clearing that threshold and appears more occupationally diverse for reasons that have nothing to do with diffusion. Control for regional usage volume and every measure of breadth I tried collapses, while the main finding stands at close to full strength.

Along the way one of my own robustness checks turned out to be worthless, in a way I think is more instructive than the checks that passed. I've written both up in Appendix B.

So breadth is not supported. That is a failure of identification rather than proof that breadth is false — the data cannot settle it either way, and I'd rather say so than dress a null up as a finding.

What this can and can't tell you

Three limits worth being blunt about.

This measures the mix, not the amount. Below the country level, the Economic Index reports what people use Claude for, not how much they use it per person — usage intensity exists only for the United States. So I can say the technical share of usage is lower in service-heavy regions. I cannot say whether less coding is happening, or the same amount of coding surrounded by more of everything else. Those are different worlds and this data cannot separate them.

This is about regions, not about the people using Claude. Service employment describes a region's workforce. The usage data describes whoever in that region is talking to Claude, and those are not the same population — Claude users are not a random sample of local workers, and nothing here links an individual's occupation to their own usage. The finding is that regions with a particular employment structure show a particular usage mix. It is not that service workers themselves use AI less technically. That distinction is easy to lose and it changes what the result means.

Nothing here is causal. These are correlations across regions at a point in time, with country fixed effects and a handful of controls. Regions differ in ways I haven't measured, and I make no claim that changing a region's industrial structure would change how its residents use AI.

What's left

What survives all of that is a fact and a question.

The fact. Within countries, the regions where you would most expect AI to be doing technical work are the regions where it does proportionally less of it. That holds across 35 countries, across the 51 US states measured on a single statistical system, across 35 refits that each drop a country entirely, and across a second measure of technical usage built from a different classification scheme with no disclosure suppression in it at all.

Why it matters. The natural way to guess where AI does technical work is to read it off the local industry mix: more offices, more technical use. Within countries the sign is the opposite. Anyone projecting regional AI effects from employment structure is working from a mapping that this data reverses.

The question. Why it runs that way, I can't tell you. Dilution is the natural candidate — technical usage looking large in industrial regions because few people there use Claude and those who do skew technical — and I tested it three ways without being able to confirm any of them. What the data can do is rule out a good deal about what the pattern isn't. What it can't do yet is say what it is.

I would rather publish a robust fact with an open question attached than a tidy story the evidence doesn't carry.

If you want to check my work

Appendix A — How the analysis was built
Data, matching, specification, and why the volume control is left out of the preferred estimate.
Appendix B — Three attempts at breadth, and a robustness check that wasn't
Why the tidy explanation could not be identified, and the argument of mine that turned out to be circular.
Appendix C — One error, four disguises
The missing-value mistake that showed up four times in two languages, and what caught it.
Full data dictionary
Every variable in the analysis, defined twice — once technically, once for a reader with no economics background.

Appendices

All three are closed by default. Each summary names what is inside, so you can go straight to the objection you actually have.

Appendix A — How the analysis was built

Data sources and vintage; how Economic Index regions were matched to OECD regions; the full accounting from 652 regions down to 279, and why the sample is 35 countries rather than 128; the exact specification; how service employment and technical usage are each defined; the control ladder for both measures; what happens under a narrower, white-collar-only definition of services, and why that is reported as a failure rather than a robustness check; where the opening's three-quarters figure comes from; why regional usage volume is deliberately not in the preferred specification; why Japan is missing; and three notes on the standard errors — the degrees-of-freedom convention, why the US-only row cannot cluster, and the Monte Carlo error on the bootstrap p-value.

Data. Anthropic Economic Index, Release 6 (June 2026), covering two monthly windows in April and May 2026. Usage composition is reported for 652 first-level administrative regions. I use the occupational breakdown, which classifies conversations into the 22 major groups of the US Standard Occupational Classification.

Matching. Economic Index regions are keyed on ISO 3166-2 codes; OECD regional statistics use OECD TL2 codes. I built a crosswalk between them from the OECD's territorial correspondence table, fuzzy-matched on both English and local region names, then hand-verified every aggregation. Regional covariates — employment by industry, GDP per capita, educational attainment — come from the OECD Regional Database via its SDMX API. US states are supplemented from the Bureau of Labor Statistics' Quarterly Census of Employment and Wages, which is finer and more current than the OECD series for the US; because US levels sit above OECD's for definitional reasons, only within-US variation is used and the country fixed effect absorbs the rest.

From 652 regions to 279

The Economic Index reports 652 subregions across 128 countries. Of those, 433 map to an OECD TL2 region through the territorial correspondence table — the rest are in countries the OECD's regional database does not cover. Requiring complete data on the analysis covariates (GDP per capita, service employment share, tertiary attainment, population) leaves 295 subregions; requiring the occupational breakdown leaves 293. Collapsing those to their parent TL2 regions, usage-weighted, gives 279 regions across 35 countries. A dozen TL2 regions are built from more than one Economic Index subregion, which is why 293 becomes 279 rather than staying flat.

Every step in that funnel is a data-availability constraint rather than a choice. Nothing was excluded on the basis of its values, and the binding constraint throughout is the labour statistics, not the usage data — the Economic Index covers far more of the world than the OECD's regional employment series does. The one case where a country was recovered by going elsewhere is the United States, where the OECD series lacks the required industry detail and QCEW supplies it.

Specification. The outcome is the computer-and-mathematical share of a region's Claude usage, measured on raw un-normalized shares. The regressor is the region's service employment share. Every specification includes country fixed effects, and the preferred one adds log GDP per capita and the share of population with tertiary education. Standard errors are clustered by country, with a wild cluster bootstrap on the key coefficient.

Defining the two key variables

Service employment follows the national-accounts convention: all employment outside agriculture, mining, manufacturing, utilities and construction. For the 34 non-US countries it comes from the OECD Regional Database's employment-by-activity series, summing the NACE Rev. 2 service aggregates — trade, transport and hospitality; information and communication; finance and insurance; real estate; professional and administrative services; public administration, education and health; arts and other services — over total regional employment. For US states it comes from the Bureau of Labor Statistics' Quarterly Census of Employment and Wages, as service-providing employment over the goods-plus-services total. A narrower variant restricted to information, finance and professional services is discussed below, under The narrower service measure.

Computer-and-mathematical usage is major group 15 of the US Standard Occupational Classification — software development, systems analysis, data science, statistics — as classified by the Economic Index. Because the Index reports each group as a percentage of the region's total usage, this share is already independent of how much of the region's data was disclosed, which is why no rescaling is applied to it.

The artifact-based measure used as an independent check sums four of the Index's 32 artifact-type shares — code_fix_or_debug, script_or_snippet, sql_or_database_query and config_or_infra — each reported as a percentage of a region's total usage. Unlike the occupational data, artifact shares are published for all 652 subregions with every category present and sum to 100 per region, so the measure carries no disclosure-suppression structure whatsoever. It averages 9.3% of usage against the occupational measure's 24.4%, and the two correlate at 0.65 within country.

Specification	Occupational	Artifact
+ country FE	−0.0748	−0.0764
+ log GDP p.c. and % tertiary	−0.0581	−0.0562
+ log usage volume	−0.0456	−0.0472

Note that the volume control is unambiguously an over-control for the artifact measure, since no disclosure channel exists for it to close. The estimate survives it regardless.

The narrower service measure, and why it is a failure rather than a robustness check

The variant mentioned above restricts services to information and communication, finance and insurance, and professional, scientific, technical and administrative activities — roughly the white-collar half of the sector, excluding retail, transport, hospitality, health and education. In the preferred specification it gives −0.1041 (t = −4.56), a larger estimate than the broad measure. It does not survive the usage-volume control: −0.0250 (t = −0.93, p = 0.35), against the broad measure's −0.0456 (t = −3.31) under the same control. Knowledge-service regions are the high-usage regions, and once volume is held fixed there is nothing left to attribute to the narrower definition.

The two measures correlate at 0.75 within country — related, as they must be, but far from interchangeable. So I report this as a failure rather than as a robustness check, because that is what it is. What it establishes is narrow but real: the result is not an artifact of the broad service category, since a genuinely different definition produces the same sign and a within-country correlation with technical usage of −0.37, essentially identical to the broad measure's −0.36. What it cannot establish is which kind of service employment is responsible.

The broader occupational aggregates

The opening claim — that professional and managerial work is about three-quarters of usage everywhere, and is unrelated to service employment — comes from the same occupational data, aggregated to SOC major groups 11 through 29 and measured on raw un-normalized shares for consistency with the headline outcome. It averages 74.9% of usage with a within-country standard deviation of 2.2 percentage points, and its within-country correlation with service employment is +0.10: effectively nothing. The computer-and-mathematical slice sits inside that block, averages 24.4%, and correlates with service employment at −0.36 within country. The contrast is not that the broader aggregate fails to vary — it varies more than the technical slice in absolute terms — but that its variation has no relationship to how service-heavy a region is.

A full data dictionary covering every variable, both technically and in plain terms, is published alongside this piece.

Robustness

The estimate survives dropping the US; dropping Washington DC; dropping the five highest-leverage regions (which strengthens it); estimating at the finer subregional grain rather than TL2; a specification without the education control, which admits two additional countries; and all 35 leave-one-country-out refits.

On Japan

Japan is absent for a mundane reason: the OECD's regional database reports total employment for Japanese regions but not the industry breakdown this analysis needs, and likewise carries no regional figures for educational attainment. Japanese usage data exists in the Economic Index and maps cleanly to OECD regions — the gap is on the labour-statistics side, and it is the same gap that required supplementing US states from a separate source.

A note on one control

Regional usage volume is a necessary control when measuring occupational breadth, because the disclosure threshold operates directly on which occupation groups appear. It is not obviously appropriate for the main result, where the outcome is always reported and has no disclosure channel, and where region size is a real economic variable correlated with service employment. Conditioning on it is arguably over-control. The preferred specification therefore omits it; the volume-controlled version is reported as robustness and the estimate survives it either way. I mention this because using different specifications in different tables without explaining why is exactly the sort of thing a reader should be suspicious of.

Three notes on the standard errors

All three were surfaced by the Stata replication.

Degrees of freedom. The reported standard errors follow the dummy-variable convention: country fixed effects are charged against the residual degrees of freedom. Because those fixed effects are nested inside the clusters, some estimators — Stata's widely used reghdfe among them — treat them as already accounted for by the clustering and do not charge them. That convention gives a standard error about 7% smaller and a t-statistic of −4.34 rather than −4.07. I report the larger, more conservative one.

The US-only row. Every other row in the robustness table clusters standard errors by country. The US-only specification cannot: with a single country there is one cluster and the cluster-robust variance is undefined. That row uses heteroskedasticity-robust standard errors instead.

The bootstrap p-value. A wild cluster bootstrap p-value is a simulated quantity, not a calculated one — it is the share of randomly drawn sign-flips more extreme than the observed statistic, so its own sampling error is meaningful at small p. The preferred specification gives p = 0.0024 with a Monte Carlo standard error of 0.0002, from 99,999 replications. An earlier run at ten times fewer replications reported 0.0028, which turned out to be the high end of the simulation noise rather than a different answer. I quote the Monte Carlo error alongside the p-value rather than implying a precision the procedure doesn't deliver.

Appendix B — Three attempts at breadth, and a robustness check that wasn't

How the privacy suppression works and how much support varies across regions; the direct evidence that the disclosure threshold moves with usage volume; three separate attempts to test the dilution story — Shannon entropy and the inverse Herfindahl, partial-identification bounds and occupation counts, and a fixed-support design — and why each failed; the argument of mine that looked like a robustness check and was actually circular, with the contamination algebra written out; and why the same control that flattens every breadth measure leaves the main finding standing.

The problem. To protect privacy, the Economic Index suppresses an occupation category in a region when the underlying counts fall below a threshold. Support therefore varies enormously: the median region reports 14 of the 22 occupational groups, and only 11 of 279 report all 22. Farming appears in 11 regions, construction in 23. Crucially, disclosure coverage is correlated with service employment, which is the regressor of interest.

You can watch the threshold operate directly. The data covers two months, April and May 2026, over an identical set of regions. April contains 6,707 occupation-group observations; May contains 8,509 — 27% more categories clearing the disclosure bar in the second month, from the same places. Nothing about the occupational structure of those regions changed in four weeks. Usage grew, and more cells cleared the threshold. That is the entire mechanism, visible in a row count.

Attempt one: diversity indices

Does a region's usage spread across more occupations as its service employment rises?

Compute Shannon entropy, H = −Σᵢ pᵢ ln pᵢ, and the inverse Herfindahl–Hirschman index, 1 ⁄ Σᵢ pᵢ², over each region's reported occupational shares — Hill numbers of order 1 and 2. Every correlation came out with the predicted sign. Raw entropy also correlates with disclosure coverage at 0.93, so it was largely measuring how much data a region disclosed.

Attempt two: bounds and counts

If diversity can't be measured cleanly, can it at least be bracketed?

Rather than adjust for the withheld mass, bound it: entropy computed under the most and least favourable assumptions about the hidden categories, which is partial identification rather than imputation. The bounds came out roughly 60% as wide as the entire cross-regional variation, so the sign follows from the assumption rather than from the data. Separately, the count of occupations with detectable usage looked strongly related to service employment until total usage volume entered the specification, at which point its t-statistic fell from 9.1 to 0.2. That count was measuring the disclosure threshold.

Attempt three: fixed support

Compare only the occupations every region reports, so nothing can be hidden.

Five SOC major groups appear in all 293 subregions. Taking the four non-technical ones as a share of all non-technical usage puts always-observed values in both the numerator and the denominator, so coverage cancels exactly rather than approximately. The statistic is built so that the null — the technical slice shrinks and everything else scales up in proportion — produces an exactly flat line, and only a genuine leak toward the long tail moves it. It was flat, in every specification that controls for volume.

The robustness check that wasn't

I had an argument for why the result could not be a data artifact. The argument was wrong, and the way it was wrong is more instructive than the checks that passed.

Early on I argued that Hill-1 and Hill-2 agreeing was evidence against an artifact. Hill-1 (entropy) is sensitive to rare categories; Hill-2 (the inverse Herfindahl) is dominated by common ones. If suppression of small categories were driving the result, the sensitive measure should move and the robust one should not. They agreed, so I took the signal to be real.

The algebra says otherwise. Renormalizing by a region's disclosure coverage C rescales every share by 1⁄C, and the two measures absorb that differently:

entropy becomes H_renorm ≈ H_raw + ln C — contaminated additively
the inverse Herfindahl becomes C² ⁄ Σᵢ rᵢ² — contaminated quadratically

The measure I had nominated as the robust one is the more coverage-exposed of the two. They agreed because both were partly measuring the same thing: how much data the region disclosed. Hill-2's robustness holds against missing tail mass, not against the rescaling — a distinction I had not drawn, and one nothing in the data would have forced me to draw. It took the bounds exercise in attempt two to expose it.

The lesson I took: a robustness check is only informative if you can state in advance what would make it fail. I couldn't, and I had let a comfortable result stand on it for longer than I should have.

What made me trust the main result

The same volume control that flattens every breadth measure leaves the technical-share finding at close to full strength. If that control were a blunt instrument destroying any relationship in the data, that asymmetry would not appear.

Appendix C — One error, four disguises

The same missing-value mistake — "we don't know" quietly becoming "zero" — in four different forms across Python and Stata: sum returning zero for an all-missing row, egen rowtotal doing the same, the case where treating missing as zero is actually correct and how to tell the difference, and Stata's rule that missing compares as larger than any number. Plus why three of the eight verification bugs made a correct result look wrong, which is the more dangerous direction.

If this project has a single transferable lesson, it is about missing values. The same conceptual mistake — letting "we don't know" quietly become "zero" — showed up four times, in two languages, wearing a different costume each time. In every case it produces numbers that look entirely plausible. Only the first one did any damage, and only because I caught the others by having been burned by it.

One. Summing nothing gives you zero

In pandas, adding up a row where every value is missing returns 0.0, not "missing." My employment data had rows where the industry breakdown was entirely absent. They summed to zero, my code then picked the most recent year with a non-missing value, cheerfully selected those fake zeros, and recorded that 29 countries had no service employment whatsoever. The fix is one argument — min_count=1 — that tells the sum to return missing when it has nothing to add. It changed results for a third of the sample.

Two. The same default, in another language

Stata's egen rowtotal behaves identically. The Stata replication had to average two monthly observations per occupation group, and the natural way to write that — add the two months, divide by two — would have silently halved the value of every group reported in only one of them. Roughly one cell in five is single-month, so about 20% of the data would have been quietly wrong. Averaging in long form instead of wide form avoids it, because that operation ignores absent rows rather than counting them as zero.

Three. The direction of the sum decides whether zero is right

This is the subtle one. Summing across months with missing-as-zero is wrong, because a suppressed month is unobserved, not empty. Summing across occupation groups with missing-as-zero is correct, because a suppressed group genuinely contributes nothing to that region's reported total. Same operation, same default, opposite verdicts — and nothing in either language warns you which case you're in.

Four. In Stata, missing is larger than any number

The verification code counted how many values exceeded a tolerance, using a comparison that is true whenever the value is missing. It reported 593 failures on a column whose largest real discrepancy was 0.000000000000000028. The only reason it wasn't believed is that it contradicted itself: the maximum difference was orders of magnitude below the tolerance while the failure count sat in the hundreds. Had the count been three instead of 593, it would have read as a genuine problem and sent me hunting through a clean build.

That last one generalises past missing values. Three of the eight bugs in the verification code made a correct result look wrong — which is the more dangerous direction, because the instinctive response is to go and "fix" something that was never broken. All three were caught by internal contradiction rather than by the check itself. The practical defence is to report several statistics per comparison — how many values were compared, the largest absolute difference, the largest relative difference, how many exceeded tolerance, whether the missingness patterns agree — instead of a single pass or fail. A single verdict can only be believed. Five numbers can disagree with each other, and that disagreement is what saves you.

Full data dictionary

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