Did Spot ETFs Break the Bitcoin Power Law?

The Two Papers

Santostasi and Perrenod (2026), A mechanistic derivation of the Bitcoin price power law: Network adoption dynamics and generalised Metcalfe scaling, published online in Elsevier's Nonlinear Science on June 29, 2026 (Vol. 8, October 2026 issue; DOI 10.1016/j.nls.2026.100172). (ScienceDirect; preprint DOI 10.5281/zenodo.19387099)

Baquero and Menezes (2026), Bitcoin's Power Law: Weak Structure, Strong Forecasts, arXiv:2605.21316v1 [stat.AP], May 20, 2026. (arXiv) A preprint, not peer-reviewed, and treated as such here.

They disagree less than the framing suggests. Both fit the same curve and get nearly the same exponent. They disagree about what that curve is.

What the Model Claims

The claim is that Bitcoin's dollar price follows P(t) ∼ t^β, where t is days since the genesis block of January 3, 2009.

The fit covers 5,696 daily observations from July 17, 2010 to February 18, 2026 — days 560 to 6,255 since genesis. Over that window the dataset spans a price range of $0.050 to $124,753 and an address count from 52,191 to 55,631,439. Prices were assembled from Glassnode plus historical Bitstamp and Coinbase data; address counts from Blockchain.com.

The headline regression, by ordinary least squares in log-log space:

log₁₀ P(t) = (−16.509 ± 0.009) + (5.690 ± 0.005) log₁₀ t,  R² = 0.961

Residual standard deviation is 0.302 dex — a typical multiplicative error of about a factor of two in either direction. That number matters later.

Two precision notes. R² = 0.961 means the regression accounts for 96.1% of variation in log-transformed price within the fitted sample. It should not be restated as “96% of Bitcoin's price is explained by time.” And the preprint abstract gives the exponent as 5.69 ± 0.05 while equation (4) and Table 1 both give 5.690 ± 0.005 — a tenfold difference in the reported standard error. If you are quoting an error bar, quote the table's.

The Claim That Got Quieter in Peer Review

This is the finding that should change how the paper is cited, and no coverage of it has noticed.

The preprint states that the exponent “is not a free parameter but is determined by two independently established physical mechanisms acting in composition.” That is a strong causal claim, and it is the version circulating in commentary, in secondary explainers, and in the arXiv critique.

The published version is more careful. It describes the price power law as “treated as the primary empirical finding; the address-count relation enters as a supporting, mechanistically motivated proxy” whose limitations as a direct measure of network participation are explicitly discussed — language that appears nowhere in the preprint. (ScienceDirect)

The published abstract also adds analyses the preprint lacked: “Stationary residuals, cointegration and out-of-sample fit rule out a spurious law.” None of those terms appears in the preprint, and the cointegration result surfaced in a Perrenod essay between the two versions (Substack, June 2026) — so the publication-stage additions answer, at least by assertion, part of what the critique demanded.

Between preprint and publication, the mechanism was demoted from derivation to supporting proxy. Reviewers appear to have pushed back on exactly the claim that makes the paper more than a curve fit — and the authors accepted the correction.

This has a practical consequence for anyone reading the debate, and a sourcing note this article owes its readers. The full published text sits behind Elsevier's paywall; the published-version language quoted above is the article page's own abstract. Every other quotation in this article comes from the preprint — where each was verified verbatim, including the limitations passage the critique cites as Section 11.3 — and section numbering may have moved in the published version.

Why It Is Not Just a Fitted Line

This is the part that distinguishes the paper from a decade of chart-drawing, and it deserves accurate statement rather than dismissal.

The exponent decomposes as β = β_A × β_M:

The composed value differs from the measured one by 0.090 — within 1.4σ of propagated error, and 1.6% of the measured value.

Each component is argued from prior literature rather than fitted to Bitcoin. β_A ≈ 3 comes from mathematical epidemiology: Colgate et al. (1989) found cumulative US AIDS cases grew as t³ rather than exponentially, deriving cubic scaling from contact-network structure, with Bacchetti and Koch (1989) confirming it by a model-independent argument. β_M ≈ 1.84 is a generalised Metcalfe relationship sitting between Sarnoff's linear-in-N and Metcalfe's quadratic-in-N, consistent with Odlyzko and Tilly's argument that per-connection value falls as networks grow, and with Wheatley et al. (2019), who found ≈ 1.69 for Bitcoin.

Three further tests are reported: a direct collapse test of the scaling identity across 5,298 observed price ratios recovering β* = 5.59; a rolling stability analysis across 564 windows spanning 2011–2026 finding median β* = 5.73 with no secular drift; and a sequential Bayesian analysis converging to a posterior of N(5.729, 0.013²) whose standard deviation follows the σ/√n asymptote without plateau, which the authors read as ruling out structural breaks at any of the four halvings.

A multi-asset control fits pair ratios for other assets. Bitcoin's binned means are straight throughout (R²_binned = 0.995); NASDAQ, the S&P 500 and gold all show pronounced curvature, with raw-pair R² of 0.434, 0.411 and 0.604 against Bitcoin's 0.907.

That is a substantive body of work. Treating it as numerology is not an honest reading.

What the Critique Actually Found

Baquero and Menezes fit 5,699 daily observations from August 18, 2010 to March 25, 2026 from the CoinDesk Bitcoin Price Index, obtaining α̂ = 5.644, R² = 0.96, residual standard deviation 0.30 — materially the same fit, with the ~0.8% gap attributed to different window endpoints. Their on-chain metrics come from a full archival Bitcoin node the authors operate themselves, explicitly to avoid aggregator inconsistencies.

The critics do not dispute the line. Their objection is to what can be inferred from it.

Their framing sentence: visual log-log linearity is a necessary but not sufficient condition for a structural power law — meaning a power law “in the sense the term has in physics: a structural invariant of the generating process, with a well-defined and shift-invariant exponent.”

They point to the proponents' own acknowledgment that “the OLS estimates assume that the power law holds throughout the entire range; likelihood-ratio tests for the lower cutoff [Clauset et al. 2009] have not been applied to the temporal series.” They also concede a technical point in the proponents' favour: the canonical Clauset–Shalizi–Newman protocol is built for distributions and cannot be transplanted mechanically onto a price-versus-time regression, so they develop time-domain analogues instead.

Their findings:

• Distributional tests. Applying CSN where it does apply — to tail-relevant series such as UTXO balances and absolute daily returns — the power-law hypothesis is rejected in the majority of tests, with log-normal preferred.
• Time-origin sensitivity. With genesis as origin, their exponent is 5.65. Shifting the origin across a plausible range drives it to 16.49 at a 5,000-day shift. Their AIC still favours the unshifted specification, so the argument is not that another origin fits better — it is that a supposed structural invariant should not depend this strongly on a modelling choice.
• Alternative forms. A three-component sigmoid stack reproduces the diagnostics offered in support of the power law and beats it in-sample.
• Direction of causation. Price changes predict on-chain metric changes more strongly than the reverse — awkward for a model in which adoption drives price.
• And then the twist. Out-of-sample, over 12- to 24-month horizons, the pure power law produces lower forecast errors than the multi-sigmoid model and than standard time-series baselines. The authors read this as a fit–prediction tradeoff: the power law's refusal to commit to particular historical wave shapes is what makes it useful at long horizons.

The critique's title is not ironic. Weak structure, strong forecasts.

The Falsification Criteria

The paper specifies five conditions under which the model would be considered broken. Quoted from the preprint:

• (F1) Floor violation. Price falls more than 3σ below the fit — “currently below approximately $10,000 in 2025” — for more than one year.
• (F2) Adoption collapse. The address growth exponent β_A falls significantly below 3 in rolling estimates.
• (F3) Exponent drift. β drifts monotonically outside [5.0, 7.0] over a multi-year period.
• (F4) Metcalfe breakdown. Price and address count decouple, measured as sustained collapse in the Metcalfe R² below 0.7.
• (F5) R² collapse. Rolling three-year R² falls below 0.80 for more than two consecutive years.

The paper states none were met over the observation period.

Three observations. These are genuinely pre-committed and measurable, which is more than most price models offer and more than stock-to-flow offered. They are also slow — F1 and F5 require sustained conditions over one to two years, so no single cycle can falsify the model, which is defensible for a long-run attractor claim but limits how much a reader should update on any quarter. And whether they still hold is unknown, because the paper's data ends February 18, 2026, before the decline discussed next.

The Prediction That Missed

It is not in the peer-reviewed paper. The paper contains no price targets of any kind. The projection traces to Santostasi's public statements in early 2024, as reported by Decrypt on February 2, 2024: “Santostasi says his model predicts that BTC will touch its cycle ‘peak’ at $210,000 in January 2026.” The figure was repeated widely through 2024 and 2025.

It did not happen, and the cleanest disproof is the proponents' own dataset. Their daily price series spans $0.050 to $124,753 through February 18, 2026. Bitcoin therefore never traded above $124,753 in the authors' own data. A January 2026 peak of $210,000 is excluded by the paper's own numbers.

Independent confirmation from SEC filings, which is where this site prefers to source prices:

Each figure verified against the filing linked on its row; all match to the cent.

The two year-end 2025 figures differ by $86.38 because they use different index providers — worth noting whenever comparing price sources. Daily series for every fund and for Bitcoin itself are on our price history pages.

Two things follow. The miss was large and real; anyone who allocated on that projection was badly served. But it does not by itself falsify the model, because the projection was not the model. None of F1–F5 references a dated price target, and a power law with residuals of ±0.302 dex — a factor of two either way — is by construction incapable of pinning a cycle peak to a month. The gap between what the model can support and what its most-repeated public claim asserted is a lesson about the promotional layer around the model, not about the mathematics.

The ETF Question

Neither paper addresses spot ETFs. Santostasi and Perrenod contain no discussion of exchange-traded products, institutional flows, or the January 2024 approvals — the approvals themselves are documented in our history of the road to the spot Bitcoin ETF. Baquero and Menezes's window fully covers the ETF era but they do not segment it, and their structural-break analysis is not framed around 2024.

That is the honest answer, and it is unsatisfying in an informative way — because the proponents identified the relevant mechanism themselves, as the first of their stated limitations:

“First, the address-count series is an imperfect proxy for participant count; exchange custodianship concentrates balances and suppresses the apparent address count relative to the true user count.”

A US spot Bitcoin ETF is exactly the structure that limitation describes. Each fund holds bitcoin through a custodian in pooled storage; the funds' registration statements name Coinbase Custody, BitGo, BNY and others, describing holdings kept in a small number of custodial wallets. Millions of end shareholders map to a handful of on-chain addresses. BlackRock's own 10-K describes each share as a fractional beneficial interest in trust assets held by custodians — economic exposure without a corresponding address.

Why a Stable Exponent Is Not Reassurance

This section is a reading of the papers' own logic. Neither paper makes this argument, and it has not been tested numerically.

Because β = β_A × β_M, ETF-mediated ownership pushes the two components in opposite directions. New participants holding through a brokerage do not create non-zero-balance addresses, so measured β_A understates true adoption growth. Those same participants' capital still moves price, so measured β_M — price per address — overstates the per-participant value relationship. The product can stay near 5.69 while both factors are biased and the mechanism underneath has quietly stopped describing what it claims to.

A stable β is not evidence that the derivation still holds.

This bears directly on the falsification regime. Two of the five criteria — F2, keyed to β_A, and F4, keyed to price–address decoupling — are measured on address count. Both would fire under genuine adoption failure. Both would also fire under a purely custodial migration of ownership off-chain, where adoption is healthy and only the measurement is broken. As written, F2 and F4 cannot distinguish those cases.

Note also that the published version's demotion of the address-count relation to a “supporting, mechanistically motivated proxy” moves the paper toward this reading. Peer review appears to have flagged the same weakness from a different direction.

What the Proponents Say

The journal paper is silent, but one of its authors is not. In an October 2025 essay, Perrenod argued that ETF and institutional custody compresses address counts relative to end-user exposure, and proposed extending the framework so that exchanges, ETFs and corporate treasury vehicles act as capital-flow channels alongside the user-growth and network-value terms — describing ETFs explicitly as new conduits for capital inflow. (Substack)

That essay is not peer-reviewed and none of its empirical figures are used here. It is cited only as evidence of how a proponent proposes to handle the ETF era: not as a break, but as an additional channel layered onto a persisting long-run relationship. That is a proposed extension, not a result in the journal paper.

Separately, and relevant to any claim that the model sailed through the ETF period untroubled: Perrenod has written that no significant bubble above the power-law trend appeared during 2025, which is why he began developing log-periodic models of the residuals. (Substack)

What the Critics Say

Baquero and Menezes make no ETF-specific claim. Their relevant objection is methodological: a continuing R² near 0.96 does not establish that the same causal mechanism is operating underneath. And on their framework the ETF question is partly malformed — if the fitted exponent already varies by nearly a factor of three across reasonable shifts of the time origin, there is no sharply defined structural constant for ETF flows to alter. You cannot detect a shift in a quantity that is not specification-robust to begin with.

Where This Leaves the Question

The descriptive relationship has not obviously broken. Two independent datasets extending into 2026 produce exponents in the mid-5s and R² around 0.96. Post-2024 observations are already inside both samples, so there is no gross break coinciding with ETF approval.

That does not establish it as a structural law. The proponents offer a decomposition and stability tests; the critique shows alternative structures reproduce the key diagnostics and that the exponent is not shift-invariant. The published version of the proponents' own paper is more cautious about the mechanism than the preprint everyone quotes.

The ETF hypothesis is untested. Nobody has isolated post-January-2024 data, re-estimated the exponent against an ownership measure that captures custodial holdings, and reported whether it moved. The primary-source record supports neither “ETFs broke the power law” nor “the power law proved ETFs don't matter.”

And the most useful open question is one the paper structurally cannot answer. F1 and F5 are keyed to conditions measured over one to two years. The paper's data ends February 18, 2026. Bitcoin fell from $87,463 at the end of 2025 to $58,745 by June 30, 2026 on SEC-filed figures. Whether the rolling three-year R² has begun to move is a calculable question, and as of this writing nobody has published the answer.

This site's own tools stay on the arithmetic that holds regardless of which camp is right: what your shares are worth in Bitcoin terms, and what fees do to that over time — see the fee-drag calculator.

FAQ