Residual Detectability Reporting: fifteen reported effects, one free parameter

Residual Detectability Reporting: fifteen reported effects, one free parameter Methods companion to "Model-family selection and recovery-gate design in generator-based noisetomography", doi:10.48550/arXiv.2611.11748. This note borrows that paper's decision variable - aresidual divided by its own standard error - and none of its derivations, so nothing here dependson the coherent-noise assumption the paper makes. Every number below is rebuilt from a publicdeposit. A residual with an error bar says how well the residual is measured. It does not say whatresidual the same run could have distinguished from zero, and the two numbers are related by afactor that can be computed before any data are taken. This deposit proposes a reporting rulefor that missing number, names it, applies it to fifteen reported effects, and checks thearithmetic eight ways. THE RULE (1) rho = r/S residual relative to its own signal (2) MDR = lambda_req * sigma_r smallest residual the run could resolve lambda_req = z(1-alpha/2) + z(beta) = 2.801585 at two-sided 5%, 80% power (3) D = MDR/r what the number is Five reporting clauses: RDR-1 report N, the shots behind the quoted number, per circuit or per point RDR-2 report r in absolute units and rho = r/S, naming S RDR-3 report MDR with alpha and beta stated RDR-4 report D; when D > 1 the number is an upper bound, and "consistent with" is not available at that budget RDR-5 report N*, the shots that would decide the effect actually claimed RDR-5 is a corollary of RDR-4 only while the standard error falls as N^-1/2, where N* = D^2 N;once a systematic term sets a floor the corollary fails and N* can diverge. THE NAME Residual Detectability Reporting, RDR. Three words, each doing work. "Residual" because the claim under audit has the form "this model's residual is small"; therule says nothing about benchmarks that quote no residual. "Detectability" rather than "significance": a significance test asks whether the null can berejected at effect zero, while the question here is the smallest effect at which the testwould reject at a stated rate. The two differ by the power, and power is the number that isusually absent. This is the reporting twin of the minimum detectable effect size familiar frompower analysis, with one difference of placement: the older literature computes it beforehand,to size a study; RDR asks for it afterwards, next to the number it bounds. "Reporting" rather than "standard": nothing here has been adopted by a journal or required byan editor, and calling it a standard would misdescribe its status. The appropriate first movefor a rule with no adopters is to name it so that it can be referred to, not to claim that itbinds anyone. The abbreviation reads in a sentence ("under RDR-4 this is an upper bound") and does notcollide with MDR, the quantity it requires. THE TABLE Fifteen rows, each divided by its own signal so that a fidelity, a relative deficit, a logicalerror and a correlation share a column. Two rows are null settings of one of the four publicdeposits, recomputed here; thirteen come from those four, unmodified. Because both MDR and theeffect are proportional to the same standard error, D = lambda_req/z exactly: the table has onefree parameter, and any row can be checked with a division to the digits printed. That is worth stating plainly. D is z rescaled by a constant, so D > 1 only restates that the runhad under 80% power at the effect it reports, which the significance already says; it is notoffered as a new statistic. The column that is not redundant is MDR - in the units of theexperiment and fixed by the design rather than by the value measured, it says what the same budgetcould have resolved. In this table the partition also coincides with ordinary significance: thelargest z among the eight is 1.49, the smallest among the seven is 3.11, and no row falls between1.96 and 2.80 - the window in which a number is significant at 5% and still below the resolutionof its own budget. The fifteen rows have none, and one of the deposits has three. Its 25 design entries sit behindrows 6-8: computed the way those rows are computed, three of them give z = 2.33, 2.37 and 2.42(p = 0.020, 0.018, 0.016) with D = 1.20, 1.18 and 1.16, so each reports an effect its budget couldnot resolve, N* of 2744 to 2971 shots against the 2048 taken. They are missing from the tablebecause the rows pool those entries by two-qubit depth and pooling is not neutral: the 58-CZ poolholds one entry at z = 2.33 and one at z = -0.97 and returns 1.48. The two deposits behind rows9-14 put nothing in the window either - 20 distance-round cells and 9 arm-axis cells, all outsideit - and the fourth is row 15 itself, at D = 17.3. window_demo.py prints all 25 entries, the threein the window, and the pools, so the count can be checked rather than believed. No row uses the source's own error bar as sigma. Twelve of the thirteen effects are either thedifference of two numbers the deposit writes (A, B) or a number re-decoded from the depositedbitstrings and counts (C, D); the thirteenth (E) is the difference the source itself quotes. Eachsigma is rebuilt from the same shot count, which is what makes a fidelity, a rate and acorrelation comparable. In E alone the rebuilt bar can be checked:0.00432 against the se(F) = 0.0043 the source computes from the same correlators, 0.5 percentapart; against the +-0.004 it prints the gap is 8 percent, which is the rounding of that digit. -- zero-rotation null D = 0.13 (resolves 5.26%) feedforward-off null D = 2.08 (upper bound 1.55%) A three devices, 4096 shots D = 5.6, 10.1, 1.9 B three depths D = 0.42, 0.15, 1.89 (58 CZ: its own MDR, 19.3%, exceeds its own effect, 10.2%) C five code distances D = 0.20, 0.36, 0.90, 2.80, 2.80 D mean Bloch X, corrections off D = 0.54 (N = 6 circuits x 8192) E the comparison the bar tests D = 17.3 (MDR 1.31% vs effect 0.076%) Eight of the fifteen have D > 1. That is the entire result, and it is a statement about budgetsrather than about anyone's arithmetic: every number is reproduced from the source, one of themto 5e-5. No row is a finding of error. The row that first made the case is the feedforward-off null. With the conditional corrections switched off,8192 shots put the MDR at 1.55% and the measured deviation from one half is 0.745%. Thedefensible sentence is "any polarization above 1.55% is excluded", not "the output isunpolarized". The same 8192 shots, asked a different question under no rotation, return 5.26%with an MDR of 0.69% -- a number those counts do resolve. The note, three pages, applies the same rule to five public device datasets (panels A-E, 5.2e5shots from four groups, nothing run for that analysis) and reports what each number carries: ascalar that is a projection, a residual without a scale, a number without its floor, and oneconfirmation that the readout product is multiplicative to 0.35 pt. WHERE THE IDEA SITS Four steps; the first three are published work by others. 2014 Wallman & Flammia, NJP 16, 103032 -- rigorous confidence bounds for randomized benchmarking, and how many sequences are needed to earn them 2017 Blume-Kohout et al., Nat. Commun. 8, 14485 -- per-scalar 95% intervals from the Hessian, with the explicit remark that a joint region over 34 parameters would cover only 17% 2025-26 four attempts to fix the scale: van den Berg (arXiv:2512.08165, stop adding terms when the misfit is within 3x the expected shot-noise misfit); Severin (arXiv:2605.00626, likelihood ratio normalised by its Wilks scale, threshold 1.65, called a convention); Di Giovanni (PR Applied 24, 044043, how a fixed shot budget is best split); Pathumsoot (arXiv:2508.12822, finite-shot MSE decomposition) 2026 this note -- the smallest effect the budget could have resolved, printed beside the effect Works 1 and 2 made the interval honest; works 3-6 made its scale explicit - four attempts at onestep, the third. None of the six reports the resolution, so a reader of any of them can see howlarge a number is and not how small a number the run could have contradicted. Entry 7 adds noarithmetic to the six; it is the fourth step, and it is a division. WHAT IS NOT CLAIMED Not an error in any of the fifteen rows. Not a random sample: the rows are the datasets whosecounts we could obtain and the six works are those whose methods we could read, so noprevalence claim follows from eight out of fifteen. Not a decision between model families. Nota claim of adoption. The factor 2.80 is a convention: at 90% power every MDR grows by 1.16,eight rows stay above their effect, a ninth (d = 7) moves from 0.90 to 1.04, and the conclusiondoes not turn on the choice. CHECKS verify_audit.py does not import the table builder and runs eight checks: V1 lambda by closed form 2.801585219 V2 lambda by bisection on erf 2.801585218 (agree to 1e-9) V3 Monte Carlo, 4e5 draws: type-I error 0.0494, power at effect = MDR 0.8021 V4 D = lambda/z on all fifteen rows, rebuilt from the archived JSON; largest disagreement 4.6e-5, which is rounding in the stored values V5 raw counts: 4035/8192 gives 49.2554% (binomial s.e. 0.5524%); 337/81920 gives 0.4114% at d = 3; 2.8016 sigma_F gives 1.2103 pt V6 the three B depth groups recombine with inverse-variance weights to 10.219988%, the same value as pooling the 25 instances directly, to 1e-9 V7 at 90% power lambda = 3.241516, a factor 1.157 on every MDR; eight rows stay above their effect, a ninth (d = 7) crosses from 0.901 to 1.042, no other row changes side V8 each row's N against the shots its own quantity uses, not the size of the deposit: 6 of the 18 circuits in D, 3 bases