The paper gives traders a restriction with nowhere to hide: two separately measured exponents must equal θ/2. Suppose the execution-weighted tail of portfolio residence scales has index θ. The tail exponent of representation-spell durations and the decay exponent of signed order-flow covariance should then coincide at θ/2. There is no free parameter between the datasets. Aggregate autocorrelation by itself leaves the restriction untested.
One threshold drives the result
Rodríguez Domínguez treats replacement of a predictive representation as a costly decision. The representation might be a factor set, a common-driver subspace or a production model version. A portfolio retains its incumbent until evidence favouring an alternative reaches threshold κ. That evidence follows reflected Brownian motion with volatility σ.
The first-passage result is τ = R²τ₀, where R = κ/σ, with Laplace transform sech(R√(2s)). The square does the work. If residence scales have tail θ, residence times inherit tail θ/2. Matching the duration tail directly to the scale tail produces a factor-of-two error.
During each spell, the chosen representation fixes a persistent conditional component of desired signed demand, even though individual trade signs may flip. Renewal aggregation over many portfolios carries the cross-sectional tail of residence scales into the decay of aggregate flow covariance. For 0 < θ < 2, covariance is non-summable and partial-sum variance has order T^(2−θ/2)L(√T).
Observed flow weights portfolios by q²λ²v: squared quantity per execution, squared execution intensity and the variance of representation-conditioned demand. Any finite cross section eventually runs out of power-law range. Under the truncated-Pareto benchmark, the window ends near the square of the largest residence scale. With N i.i.d. Pareto draws, that proxy grows as N^(2/θ).
There is no market data here.
The evidence comes from Monte Carlo paths generated by the author's own model. Seed 260902 is used for three tail indices θ ∈ {0.8, 1.2, 1.6}, with 30 replications, 500 portfolios and 4,096 observation periods. Each spell-tail estimate also receives an independent 30,000-duration sample.
Recovery works for two targets
The first two simulated flow exponents closely match the restriction. A target of 0.400 produces a mean of 0.409 and Monte Carlo standard error 0.009. At the 0.600 target, the mean is 0.603 with SE 0.014.
The implementation is specified in enough detail to inspect. The exit clock uses 48 explicit exponential components, followed by a moment-matched gamma remainder. Pools contain 200,000 first-exit draws and 200,000 equilibrium-residual draws, and every renewal process begins in equilibrium. For the exit draws, the diagnostics report mean 1.001 and variance 0.668 against a theoretical mean of 1. Equilibrium residual draws have mean 0.833.
Performance deteriorates at the 0.800 target. The mean reaches 0.898 with SE 0.041, while the 10th to 90th percentile range spreads across [0.670, 1.217]. On the same design, the duration estimate is 0.801 with SE 0.003.
The author calls out the problem directly. Near the short-memory boundary, this flow estimator needs either a longer horizon or an explicitly bias-corrected design. The range [0.670, 1.217] crosses α = 1, which separates summable from non-summable covariance. With 500 portfolios, 4,096 periods and a log-log regression over lags 24 to 256, the flow estimate cannot determine which side contains the process.
The tuning choices
Flow decay is estimated by log-log regression over lags 24 to 256. Duration tails use a Hill estimator applied to the largest 8% of 30,000 draws. The usable-horizon statistic ends at the final point in the first run of local log-slopes that remain within 0.20 of θ/2, requiring five consecutive observations before entry or exit.
Each rule is stated precisely. The reported results provide no sensitivity check for any of them.
Another implementation choice concerns transitory demand. Equation (9) permits a component ε alongside persistent demand, while Assumption 3 requires its normalised covariance to remain lower order than the persistent tail. In simulation, every portfolio receives a centered binary spell state and the protocol aggregates executed signed states. No explicit ε component is added.
Execution weights carry the economics
The misalignment experiment fixes θ = 1.6 and lets execution intensity increase with residence scale according to R^η exp(0.2Z). As participation elasticity moves from 0 to 0.300, the execution-weighted target declines from 0.800 to 0.500. Aligned mean estimates follow it, moving from 0.803 to 0.507. Across the same range, unweighted estimates remain between 0.797 and 0.804.
That stable unweighted figure answers a different question.
A duration tail estimated from account counts will generally test the wrong restriction when it is compared with an exponent estimated from executed flow. The paper also reports that the aligned estimator grows unstable at larger elasticities because the effective sample thins. The prescribed response is an effective-sample-size warning, rather than a forced exponent claim.
How long can the scaling survive?
At θ = 1.4, using 60 draws per size, the median usable scaling horizon rises from 68.539 periods for 100 portfolios to 12,270.751 for 3,000. Throughout, the realized stable range falls short of the largest-residence-scale proxy.
Those medians imply a factor of about 179 across a 30-fold increase in population. The N^(2/θ) proxy at θ = 1.4 predicts about 129. Dispersion remains wide. The paper recommends estimating the cutoff from stability across lag windows and cross sections, while treating the largest observed residence as an upper-scale diagnostic. It reports no usable-horizon figure for the 500 portfolios in the exponent-recovery experiment.
The paper closes off a tempting shortcut as well. Conditioning both observations on their membership in the same spell removes the survival probability responsible for the decay. The flow exponent must therefore be estimated from unconditional aggregate covariance. Within-spell comparisons serve only as alignment tests.
Evidence the test still needs
We could not test the restriction. Its protocol requires dated account-level representation states, signed executions and reconstructed parent orders so that the order-splitting channel can be stripped out. We have OHLCV bars, without trade prints or participant identifiers. The binding data gap is the join between an account's model-version history and its executions.
The paper does not claim this channel dominates. It tabulates four persistence channels, order splitting, representation residence, common regime and self-excitation, each with different binding controls. It also concedes that aggregate autocorrelation cannot distinguish among them.
A firm holding versioned production models, account identifiers and its own execution records would have the required inputs. It would apply identical execution weights to residence spells and signed flow, estimate duration tails on a training sample, then evaluate unconditional flow covariance and its cutoff on held-out observations.
One institutional test would change my view: run the protocol on an internal model-change log and signed fills, control for parent orders, and report the held-out difference 2α_F − θ. The θ/2 mapping is derived analytically through first-passage renewal analysis, then checked against realized simulated paths. Market-data validation remains absent, exactly as the author acknowledges: "They remain structural validation, not market evidence."