Urban Scaling of Disease, Mortality and Crime in the United States

Framing (non-negotiable). Cross-sectional ecological analysis of US census places (n = 26,343) and counties (up to 3,072 per outcome, from 3,196 joinable county nodes), using model-based small-area health estimates, county vital-statistics summaries and federal court records. Level of inference is population-level association between settlement size and outcome burden — not individual risk, and not causal. Every exponent below describes how a count co-varies with population across places at one point in time; it does not describe what happens to a given city as it grows. Keep this caveat attached to every downstream claim.

Abbreviations. β = scaling exponent in Y ∝ N^β; N = population; Y = outcome count; CI = confidence interval; OLS = ordinary least squares; CDC PLACES = CDC Population Level Analysis and Community Estimates; CHR = County Health Rankings; YPLL = years of potential life lost (before age 75); RUCC = Rural–Urban Continuum Code; FIPS = Federal Information Processing Standards (geographic code); CBSA = Core Based Statistical Area; IDB = Integrated Database (federal court records); MAUP = modifiable areal unit problem; KG = knowledge graph; MRP = multilevel regression and poststratification; NCD = non-communicable disease.

1. Executive summary

Across 18 outcomes assembled from 3 OKN knowledge graphs, there is no single urban scaling law for health. The outcomes separate into three regimes. The separation is not a matter of statistical power: the place-level exponents are estimated to within a few thousandths and the county-level ones to within roughly one to four hundredths, so the differences between regimes are far larger than the uncertainty on any individual estimate.

Mortality scales robustly sublinearly. Larger US counties have systematically fewer deaths than proportionality predicts, and this is the one result that survives every robustness test applied. Premature death (YPLL) scales as β = 0.924, child mortality at 0.839, infant mortality at 0.858, and motor-vehicle crash deaths most steeply of all at β = 0.736 — a county ten times larger has roughly 45.6% fewer road deaths per capita. Six of the eight mortality measures keep the same direction and significance when the sample is restricted to metropolitan counties; the two exceptions, drug-overdose and alcohol-impaired driving deaths, lose significance in the smaller sample rather than changing direction. This is the classic "urban health advantage," and it is the finding a reader should take away with most confidence.

Chronic-disease scaling depends entirely on the minimum size required of a "city". Fitted over all 26,343 census places, the nine chronic conditions look mildly sublinear or linear (β = 0.963–1.002). Restricted to the 709 places above 50,000 people — closer to what the urban-scaling literature means by a "city" — six of the nine flip to superlinear: diabetes rises from β = 0.996 to 1.078, stroke from 0.985 to 1.063. A threshold ladder (Figure 3) shows the exponent climbing as the size cutoff rises — substantially, though not monotonically. The exponent here is a property of the size cutoff used to define a city, not of the urban system, and we grade all six of these outcomes Tier C accordingly.

Crime is the weakest result, and it does not reproduce the canonical superlinearity. Federal criminal case filings scale at β = 0.803 over all counties but at 1.048 (CI 0.990–1.105, indistinguishable from linear) among metropolitan counties. Federal caseload is a poor proxy for crime — it is driven by prosecutorial jurisdiction, border districts and tribal-land coverage — and its rate regression explains under 5% of variance. We report it as a bounded null, not as a refutation of the literature's β ≈ 1.16 for local violent crime.

The overarching quantitative caution: population size explains very little of the variance in outcome rates. Across all 18 series the rate-regression R² ranges from 0.0005 to 0.439; only motor-vehicle deaths exceed 0.30. Scaling exponents can be precise and still describe a weak relationship, and the two properties are routinely conflated.

2. Sources used

No other knowledge graph contributed a number to this report. Graphs inspected during scoping but not used (nikg, single-city Philadelphia incident data; biohealth; spatialkg) have no logged query and therefore no row here.

3. Design & rules

The analysis estimates the urban scaling exponent β in Y ∝ N^β, where N is settlement population and Y is the count of an outcome. β = 1 means the outcome is a fixed share of population; β > 1 (superlinear) means larger settlements bear disproportionately more; β < 1 (sublinear) disproportionately less.

Two design choices deserve a reader's attention. First, the OKN sources supply rates, not counts, so counts are reconstructed as rate × population. This makes population appear on both sides of the regression, which mechanically forces the count-regression R² close to 1 — a well-known trap. We therefore report the rate-regression R² (of ln(Y/N) on ln N, whose slope is exactly β − 1) as the honest measure of explanatory power, and never quote the count R². Second, spoke-okn place records carry their own population field, so the place-level analysis needs no cross-graph join at all; only the county-level arms join to ruralkg, using the federation's pre-verified K2 county-FIPS crosswalk rather than a hand-built key.

Because the endpoint is QLever and supports math:log, all regressions were computed from sufficient statistics aggregated server-side — n, Σx, Σy, Σx², Σxy, Σy² per outcome — rather than by extracting 237,087 rows. The closed form is algebraically exact; the practical limit is that the endpoint returns each sum at six significant figures, which propagates ~10⁻⁴ into β (quantified in §6.3). That is immaterial for the county arms, whose standard errors are 4–40 times larger, but it is a non-trivial fraction of the place-arm standard errors and is carried as limitation 7.

The crime arm carries a structural caveat that no statistic can repair. scales records federal district-court cases; the vast majority of US crime is prosecuted in state courts. Federal caseload therefore reflects federal enforcement priorities and district geography — immigration cases concentrate on the southern border, and federal jurisdiction over tribal land inflates counts in otherwise small counties. We keep the arm because it is the only cross-county justice measure in the federation, and grade it accordingly.

Inventory rebuilt live from the logged queries:

The place sample spans more than five orders of magnitude of population, but panel (B) shows the mass sits between 100 and 10,000 — only 709 places exceed 50,000. Any exponent fitted over the whole range is therefore dominated by small settlements, which is precisely the sensitivity §5.2 exploits.

4. Confidence tiers

Tiers grade how stable an exponent is under a change in the definition of a city, not how precisely it was measured — every exponent here is precise. Each outcome was re-fitted on a restricted sample (places ≥ 50,000; or metropolitan counties, RUCC 1–3) and compared with the full-sample fit.

Two honest caveats about this scheme. The restricted samples are 10–37× smaller than the full ones, so their standard errors are 6–18× wider; a Tier B grade can therefore reflect lost statistical power rather than a genuinely marginal effect. And the tiers are assigned by whether each sample's CI crosses 1, not by a formal test of whether β differs between samples — no such test was performed. Distribution across the 18 series: Tier A = 7, Tier B = 5, Tier C = 6. Every Tier A result is a mortality measure except one; every Tier C result is a chronic disease. That split is the report's central finding.

5. Findings by axis

5.1 Primary signal — the exponent spectrum

Fitted over the full sample, the 18 outcomes span β = 0.736 to 1.002. Only one outcome is classified superlinear in the full sample — high cholesterol, β = 1.0017 (CI 1.0012–1.0023) — and it exceeds linearity by less than a fifth of a percent. With n = 26,343 a deviation that small is comfortably detectable, so the classification is statistically correct but substantively negligible; we read it as linear throughout the discussion.

The ordering is informative. The steepest sublinear scaling belongs to motor-vehicle crash deaths (β = 0.736) and federal criminal filings (β = 0.803) — both plausibly geographic rather than epidemiological, reflecting rural road exposure and federal district structure respectively. Child and infant mortality follow (0.839, 0.858), then the broad mortality measures near 0.92–0.96, then the chronic diseases clustered tightly just below 1. The chronic-disease cluster's tightness against β = 1 is exactly what one expects when the outcome is a near-constant fraction of the population — and it is what the next axis dismantles.

5.2 City definition — the exponent is not a fixed property

Re-fitting each chronic condition on progressively larger minimum-population cutoffs produces a systematic drift, not noise.

All nine curves rise substantially between the lowest and the highest usable cutoff, and eight of the nine cross β = 1 at some cutoff — only depression stays below 1 throughout. None rises monotonically, however: each dips across part of the small-place range — asthma from 0.996 to 0.988, depression from 0.985 to 0.967 — before climbing, so the curves are V-shaped in the cutoff rather than steadily increasing. Diabetes moves from 0.996 across all places to 1.075 at a ~60,000 cutoff (and 1.078 in the separate ≥50,000 refit reported in §5.4) — a swing far outside any single fit's confidence interval. The drop at the last cutoff reflects n falling to 139 places and should not be read as a reversal. Note also that the rungs are nested subsamples, not ten independent observations, so the ladder is one coherent piece of evidence rather than ten. The practical implication is blunt: an analyst who defines "city" as population ≥ 50,000 will report superlinear chronic-disease scaling, and one who includes all census places will report sublinear scaling, from identical data.

5.3 Functional form — the relationship is not a power law

The drift in §5.2 has a direct explanation: the log–log relationship is curved, so no single exponent describes it.

Diabetes and stroke trace a clear U-shape: prevalence declines gently through small and mid-sized places, reaches a minimum somewhere around 30,000–100,000, then rises sharply among the largest cities, and both have positive fitted curvature (diabetes significantly so, stroke marginally). Hypertension and asthma show the same late upturn in the binned means, but their fitted global curvature is significantly negative — so for those two the upturn is a local feature of the large-city tail, not the shape of the whole curve, and calling them U-shaped would misdescribe the fit. Obesity and depression decline over most of the range. A quadratic term in ln N is statistically significant for six of nine conditions; with n = 26,343 that test is close to vacuous on its own, and the global quadratic disagrees in sign with the size-stratified fits for several conditions. The stratified estimates in §5.2 are therefore the primary evidence and the quadratic is reported only as a test against the power-law form, not as a source of local exponents.

5.4 Robustness — restricted samples

Panel (A) is the Tier C result made visual: every chronic condition moves right, and six cross the line. Panel (B) is the Tier A result: the mortality measures barely move, holding their direction and significance, with only drug-overdose and alcohol-impaired driving deaths losing significance in the smaller metropolitan sample. Federal criminal filings move furthest of all — from clearly sublinear to indistinguishable from linear — which is consistent with the jurisdictional confound in §3 rather than with a genuine scaling effect.

6. Domain analyses

6.1 Mortality — the urban health advantage

The six mortality measures at Tier A form the report's most defensible claim. Reading β − 1 as a rate elasticity — a comparison between counties, not a change within one — a county ten times larger than another has on average a 16.0% lower premature-death rate, 31.1% lower child mortality, 27.9% lower infant mortality, and 45.6% lower motor-vehicle death rate. The gradient is steepest for causes with a strong exposure component (road deaths) and for outcomes sensitive to healthcare access (infant and child mortality), and shallowest for the broad age-adjusted mortality measure. This ordering is consistent with a services-and-access explanation — larger counties concentrate hospitals, trauma centres and specialist care, and have less per-capita exposure to high-speed rural road travel — but no covariate measuring access or road exposure was entered into any model here, so that reading is a hypothesis suggested by the ordering, not a result of it.

Two of the eight CHR measures are excluded from the count-scaling interpretation and reported only as rate elasticities: alcohol-impaired driving deaths is a proportion (share of driving deaths), not a population rate, so multiplying by population does not yield a count; and infant mortality uses live births rather than population as its denominator, making its reconstructed count approximate. Child mortality has the same denominator caveat in weaker form. These are flagged rather than dropped because their direction is consistent with the rest of the family.

6.2 Chronic disease — a definition-dependent result

We ran the scaling fit for all nine conditions available in CDC PLACES via spoke-okn; none was skipped. The full-sample result (mild sublinearity) and the restricted-sample result (superlinearity for six of nine) are both reported because neither is privileged — the honest statement is that chronic-disease scaling in these data is not identified without a prior commitment to what counts as a city.

One mechanism deserves flagging as a limitation rather than a finding. CDC PLACES estimates are model-based small-area estimates produced by multilevel regression and poststratification, which borrow strength from demographic and socioeconomic covariates. Where those covariates themselves vary with settlement size, some of the apparent size gradient may be induced by the estimation model rather than observed. This does not affect the relative comparison between cutoffs in §5.2 — the same estimates are used throughout — but it does mean the absolute exponents should not be treated as if they came from direct measurement.

6.3 Method verification

The sufficient-statistics approach was checked against a direct fit on extracted rows. For diabetes in the 139 places above 162,755 population, a client-side OLS on the raw (population, prevalence) pairs gives β = 1.012098 (SE 0.027505); the sufficient-statistics route on the same rows gives β = 1.012098 (SE 0.027505), agreeing to 6.4 × 10⁻¹⁵. The independently aggregated SPARQL band-ladder gives β = 1.012227, differing by 1.3 × 10⁻⁴ — attributable to the endpoint returning sums at six significant figures, and negligible against a standard error of 0.027.

7. Discussion

The three regimes point to different mechanisms, and the report's structure is an argument that they should not be pooled into a single "urban scaling law for health."

Mortality's robust sublinearity is most readily interpreted as an infrastructure and access pattern (untested here, since no such covariate entered the models). It behaves like the classic sublinear urban quantities — road length, infrastructure per capita — rather than like the superlinear socioeconomic ones, and it is insensitive to how the urban unit is drawn, which is what one expects of an effect operating through service provision rather than through interaction density.

Chronic disease's instability is best read as a measurement result rather than a substantive one. The U-shape in Figure 4 suggests two opposing gradients: a socioeconomic gradient making mid-sized suburban places healthier than small rural ones, and a large-city gradient — deprivation, segregation, the concentration of poverty in central cities — accompanying the rise in prevalence above roughly 100,000. Census places cut through functional metropolitan areas, separating central cities from their suburbs; a metropolitan-area analysis would pool them and could plausibly show neither pattern.

This yields three testable predictions. First, re-running the chronic-disease arm on CBSA-aggregated metropolitan areas should attenuate the superlinearity seen above 50,000, because the central-city/suburb split is what generates it. Second, conditioning on median household income or the Gini index — both present in spoke-okn's SDoH layer — should absorb most of the large-city rise in diabetes and stroke. Third, an infectious-disease outcome, if one were added to the federation at place level, should show superlinearity that is stable across cutoffs, since contact-driven transmission is the mechanism the superlinear literature actually describes, and chronic disease is not.

8. Comparison with prior work

Claims were checked against the primary literature retrieved through the PubMed and Paperclip MCP connectors. The full per-claim record, with citations, is in Urban-Scaling_literature_comparison.md.

Claims 1, 2 and 5 were checked against full article text; the remainder were assessed from abstracts and, for claims 3 and 4, from the papers' reported conclusions. Four labels were downgraded during review (claims 3, 4, 7 and 10) after checking whether the cited work performed the same operation as this analysis — in each case it did not, and the reasons are in the Concordance cells.

Where the KG evidence diverges from the literature. Two divergences are matters of scope, not error. Our crime result (claim 5) diverges because scales measures a different object than the literature's police-recorded crime — a data-coverage limitation of the federation, not a contradiction of prior findings, and the honest response is the UNRESOLVED label rather than a claim of refutation. Our chronic-disease result (claim 2) diverges from itself depending on the cutoff, which the literature (claims 3, 4) predicts it should. We found no evidence of an error in the underlying graphs: the one genuine data-quality observation is that spoke-okn's PREVALENCEIN_SpL stores County Health Rankings values in two different string encodings — bare numerics and value(quartile) pairs — within the same predicate, which silently drops five of eight mortality measures from any query that assumes a single format. That is a parsing hazard rather than a factual error, and is documented in the reproducibility record.

9. Full ranked results

The complete table of 18 fitted series — with exponents, confidence intervals, rate elasticities, honest R², restricted-sample refits and tier assignments — is in Urban-Scaling_results.xlsx (sheet Ranked Results) and data/ranked_results.csv. The threshold-ladder refits and the per-band sufficient statistics are in the same workbook.

Sort by any column, filter with the search box, or use the drop-downs to isolate a tier, a domain or a geographic level. The sources (n) column shows how many federation graphs each row depends on: spoke-okn supplies every outcome measurement, ruralkg the county population denominators and RUCC classification, and scales the crime counts.

The ranking makes the tier structure legible: the six Tier C rows are all chronic diseases whose direction reverses between samples, and they cluster tightly around β ≈ 0.96–1.00 in the full sample — close enough to linearity that a reader seeing only the full-sample column would reasonably conclude "chronic disease scales linearly," which §5.2 shows to be an artefact. The Tier A block, by contrast, spans β = 0.736 to 1.002 and holds its ordering under restriction.

10. Summary of findings & limitations

Findings recap. Mortality in US counties scales sublinearly with population, robustly and across every measure tested: premature death at β = 0.924, child mortality at 0.839, motor-vehicle crash deaths at 0.736. This is the study's Tier A result and it corroborates the published finding that larger US cities have lower mortality. Chronic-disease scaling is not identified without a prior minimum size for a "city": the same nine CDC PLACES conditions give β = 0.963–1.002 across all 26,343 census places but β = 0.995–1.078 across the 709 places above 50,000, with six of nine reversing direction, and eight of nine crossing β = 1 somewhere on the threshold ladder. Crime, measured through federal court filings, gives β = 0.803 overall and 1.048 among metropolitan counties, and is too confounded by federal jurisdiction to test the literature's superlinear finding. Across all 18 series, population explains between 0.0005 and 0.439 of the variance in outcome rates.

Limitations.

1. Ecological, cross-sectional, non-causal. These are associations between settlement size and outcome burden across units at one time. No individual-level inference and no claim about what happens to a city as it grows is supported; claim 8 in §8 makes this explicit against the literature.
2. Census places and counties are not functional cities. The urban-scaling literature fits metropolitan areas. Neither administrative unit used here corresponds to a functional urban system, and §5.2 demonstrates the consequences directly. A CBSA-level re-analysis was not possible because the federation carries no county→CBSA crosswalk; the RUCC metropolitan restriction is a proxy, not a substitute.
3. CDC PLACES prevalence is modelled, not measured. Estimates come from multilevel regression and poststratification using demographic and socioeconomic covariates, so part of any size gradient may be model-induced. Only age-adjusted estimates are available, so crude prevalence scaling could not be examined.
4. Rates converted to counts. Counts are reconstructed as rate × population, putting population on both sides of the regression. We report rate-regression R² throughout for this reason, but the reconstruction is exact only where the rate's denominator is total population — which fails for infant mortality (live births), partly for child mortality, and entirely for alcohol-impaired driving deaths (a proportion), as flagged in §6.1.
5. Federal criminal filings are a poor crime proxy. Most US crime is prosecuted in state courts. Border districts and federal jurisdiction over tribal land distort the geography, and the rate regression explains under 5% of variance.
6. Mismatched vintages. CDC PLACES populations are 2010 census, ruralkg populations are 2013, and County Health Rankings values are 2023. Population changes over that span introduce noise into the county denominators; it is unlikely to be systematic with respect to size but is not zero.
7. Six-significant-figure aggregates. The endpoint returns summed statistics at six significant figures, contributing ~10⁻⁴ error to β (quantified in §6.3). Against the county-arm standard errors (0.004–0.029) this is negligible; against the place-arm standard errors (0.0003–0.001) it is 10–35% of the SE, and comparable to the entire margin by which high cholesterol is classified superlinear. Place-arm exponents should therefore be read to three decimals, not more. Note also that the sufficient statistics in data/ are computed on centred variables (x = ln N − 8, y = ln Y − 5), so they cannot be used to recover means directly.
8. Selective coverage of mortality measures — the most serious threat to the headline finding. The eight County Health Rankings measures cover 1,209–3,072 counties, not all 3,196; counties are suppressed where death counts are too small to report reliably. Suppression is by construction correlated with small population, so the smallest counties are missing precisely from the tail that would most influence the fit, and the direction of the resulting bias is toward apparent sublinearity — the same direction as our Tier A result. We could not quantify it because the suppressed counties' values are unavailable by definition. Any reader treating sublinear mortality as established should treat this as the first thing to rule out.
9. Classical standard errors only. All fits use unweighted OLS with classical standard errors. Residual variance plainly differs across five orders of magnitude of population, and no heteroskedasticity-robust or weighted alternative was computed. The reported CIs — especially the very narrow place-arm ones — are therefore likely optimistic, which matters most for marginal calls such as high cholesterol.
10. Threshold-ladder rungs are nested. Each rung is a subsample of the one below, so the ladder is a single coherent piece of evidence, not ten independent tests; and truncating the range of a curved relationship changes the fitted slope by construction (§5.3). The ladder demonstrates sensitivity to the size cutoff — it does not by itself establish that any particular cutoff is correct.
11. No infectious-disease outcome. The superlinear scaling reported in the literature is largely for contact-driven infectious conditions, none of which is available at place level in the federation, so the study cannot test the mechanism most central to the superlinear literature.

11. Reproducibility

Everything needed to replicate this analysis — the originating prompt, the replicator specification, every supporting SPARQL query verbatim with its row count, the verified quantities, and pinned KG versions — is in Urban-Scaling_reproducibility.md, with analysis scripts in scripts/ and intermediate extracts in data/.

12. References

Retrieved via the PubMed MCP connector. Full-text verification via the Paperclip MCP connector.

1. Bilal U, et al. Scaling of mortality in 742 metropolitan areas of the Americas. Sci Adv. 2021. PMID:34878846 · doi:10.1126/sciadv.abl6325 — full-text-verified (PMC8654292)
2. McCulley EM, et al. Urban Scaling of Health Outcomes: a Scoping Review. J Urban Health. 2022. PMID:35513600 · doi:10.1007/s11524-021-00577-4 — full-text-verified (PMC9070109)
3. Arcaute E, et al. Constructing cities, deconstructing scaling laws. J R Soc Interface. 2015. PMID:25411405 · doi:10.1098/rsif.2014.0745
4. Cottineau C, et al. Diverse cities or the systematic paradox of urban scaling laws. Computers, Environment and Urban Systems. 2017. doi:10.1016/j.compenvurbsys.2016.04.006
5. Sutton J, et al. Comprehensive indicators and fine granularity refine density scaling laws in rural-urban systems. Sci Rep. 2026. PMID:41741585 · doi:10.1038/s41598-026-40238-7
6. Hanley QS, et al. Rural to urban population density scaling of crime and property transactions in English and Welsh Parliamentary Constituencies. PLoS One. 2016. doi:10.1371/journal.pone.0149546
7. Bettencourt LMA, et al. Growth, innovation, scaling, and the pace of life in cities. Proc Natl Acad Sci U S A. 2007. PMID:17438298 · doi:10.1073/pnas.0610172104 — full-text-verified (PMC1852329)
8. Oliveira M. More crime in cities? On the scaling laws of crime and the inadequacy of per capita rankings. Crime Science. 2021. doi:10.1186/s40163-021-00155-8
9. Marquis U, Barthelemy M. On the Meaning of Urban Scaling. arXiv (preprint — not peer-reviewed). 2026. doi:10.48550/arXiv.2603.30021
10. Proto-OKN federated SPARQL endpoint (FRINK), queried 2026-07-25/26 via the mcp-okn MCP server; knowledge-graph versions pinned in §2.