Across-Design Uncertainty in Short Pricing Panels: Evidence from Simulated Price Trajectories

Across-Design Uncertainty in Short Pricing Panels: Evidence from Simulated Price Trajectories Pedro Cadahia Delgado∗

arXiv:2608.21334v1 [cs.LG] 21 Aug 2026

PhD, Universidad de Huelva, Spain

Abstract Short observational pricing panels can contain many observations while offering only a small number of distinct price movements. This paper studies the inferential consequences of that distinction in a synthetic data-generating process calibrated to a sparse pricing regime. We separate uncertainty conditional on a realised price trajectory from variation in estimation error across alternative trajectories generated by the same pricing process. In the baseline simulations, the latter component accounts for 97.6% of the variance of the estimation error for the gradient-boosted specification. This magnitude is a property of the simulated design, not a general constant. Within-panel resampling and cluster-robust procedures use the information contained in one realised trajectory and therefore do not, without additional modelling or independently realised trajectories, identify this across-design component. The simulations also indicate that the coverage shortfall is associated with design-specific centring error, not only with underestimated conditional variance. Three results organise the analysis. First, over the simulated grid, across-design dispersion is well described by the empirical relation σ̂b ≈ 0.182V −0.271 , where V = nmoves × magnitude2 . We treat the exponent −0.271 as a simulation regularity rather than as a theoretical scaling law. Second, adding regions that share a common price path can reduce outcome noise and improve nuisance estimation, but it does not create additional independent price trajectories. By contrast, averaging estimates across units with approximately independent√design-specific errors reduces the standard deviation of that component at the familiar k rate under the stated covariance conditions. Third, a Paule–Mandel variance component estimated across independently priced units substantially increases empirical coverage in the homogeneous simulation, from 0.469 to 0.931 for the posterior-centred variance-augmented construction; when unit-level truths differ, the same component mixes design uncertainty with genuine heterogeneity and should be interpreted accordingly. The broader implication is a shift from asking only how to refine inference on a fixed passive panel to asking how the data-generating design can create additional identifying variation. Controlled regional randomisation is one transparent way to do so, but the numerical gains reported here remain simulation-specific. Keywords: price elasticity; design uncertainty; Double Machine Learning; coverage; short panels; variance components. JEL: C33, C55, L11, M31.

∗

Corresponding author.

1

1

Introduction

Empirical pricing work often reports an elasticity estimate together with a confidence interval constructed from the realised panel. In short panels, however, the number of rows can be a poor description of the amount of treatment variation available for identifying the price coefficient. A manufacturer may observe many region–week cells while changing a common list price only a handful of times. This paper asks what conventional inferential procedures represent in that setting and what additional uncertainty appears when the realised price trajectory itself is treated as one draw from a broader pricing process. The organizing distinction is between within-design and between-design uncertainty. Let a design D denote the realised configuration of price movements and other non-shock features of the panel, and let u denote the demand shock. Conditional on D, repeated draws of u generate the familiar sampling or shock uncertainty around an estimator. Across alternative realisations of D, the estimator can also be displaced because different price trajectories provide different residualised treatment variation and different alignments with confounders. We refer to the dispersion of this design-specific centring error as between-design uncertainty. The distinction is conceptually related to the separation between sampling-based and design-based uncertainty in Abadie et al. [2020] and to recent design-based analyses of quasi-experiments [Rambachan and Roth, 2026]. Our use of the terminology is narrower: the simulations explicitly generate multiple pricing trajectories so that the two components of the estimation error can be measured separately. This distinction also clarifies what can and cannot be learned from a single realised panel. A block bootstrap, a cluster-robust covariance estimator, or a multiway-clustered covariance estimator can be appropriate for aspects of dependence and repeated-sampling variation supported by the observed data. None of these procedures is designed, by itself, to nonparametrically recover the distribution of estimator displacement across price histories that were not observed. This is not the claim that such methods are generically invalid. It is a statement about the object they condition on and about the additional assumptions or data required to learn a distribution over alternative designs. We study this issue in a synthetic data-generating process with 120 weeks, sparse list-price movements, promotions, competitor prices, calendar variables, weather and inflation. The baseline configuration has ten list-price changes per series with magnitudes between 3.0% and 7.5%. These values are chosen to be broadly comparable with empirical moments reported by Nakamura and Steinsson [2008]; the calibration is intended to place the exercise in a plausible pricing regime rather than to establish external validity for any particular category. Because the generator supplies the ground truth and permits repeated shocks within the same price trajectory as well as repeated price trajectories, it makes observable a decomposition that cannot be learned nonparametrically from one realised historical panel. The baseline simulation is deliberately stark. For the gradient-boosted specification, 97.6% of the variance of the estimation error is associated with variation in the design-specific conditional mean error; for the sieve specification the corresponding share is 99.3%. The reported bootstrap standard error is larger than the measured within-design standard deviation but much smaller than the across-design dispersion. Thus the empirical finding is not simply that one bootstrap happens to be too narrow. Rather, in these simulations a substantial part of the coverage shortfall is associated with variation in the conditional centring of the estimator across realised price histories. 2

Contributions.

The paper makes three related contributions.

1. Within-design versus between-design uncertainty. We formulate the variance decomposition on the estimation error θ̂ − θ(D) and measure its two components by holding the design fixed while resampling shocks and then repeating the exercise across designs. In the baseline DGP, between-design centring dispersion is much larger than within-design shock dispersion. The exercise shows why procedures based only on one realised panel need not represent repeated-design uncertainty, while avoiding the stronger claim that all within-panel inference is invalid for conditional questions. 2. More observations are not the same as more identifying trajectories. Adding region–week rows under a common national list price may improve estimation of outcomeside objects and reduce some conditional noise, but it does not multiply the number of independently realised price paths. More generally, the variance of an average of design-specific errors depends on their covariance. Under approximately independent, mean-zero design-specific √ errors, averaging k independently priced units reduces their standard deviation by k; under a common design component, the reduction is smaller and can disappear. This provides the formal basis for the paper’s practical message that “adding rows” is not equivalent to “adding identification.” 3. From inferential correction to data design. Across the simulated grid, the relation σ̂b ≈ 0.182V −0.271 summarizes how design dispersion changes with the heuristic variation index V = nmoves × magnitude2 . The exponent is reported only as an empirical regularity of these simulations. A variance-component construction across independently priced units improves repeated-design coverage, but it becomes wide and, when true effects differ, mixes design dispersion with genuine heterogeneity. These findings shift the practical emphasis from searching only for a more elaborate post-hoc interval toward generating additional independent treatment variation. Randomized regional pricing is one transparent design option, not a logically necessary one. Conditional and repeated-design questions. The paper reports both conditional coverage given a realised design and coverage averaged over generated designs. These answer different questions. Conditional coverage asks how an interval behaves if the observed price trajectory is held fixed and only the shock is repeated. Repeated-design coverage asks how the full estimation procedure behaves when the price trajectory is itself redrawn from the DGP. The second object is useful for methodological evaluation and for a firm contemplating future pricing histories; it should not be conflated with the first. Relation to weak identification. Sparse price movement reduces the residualised treatment variation available in the partially linear regression. This is naturally related to the broader weak-identification and weak-signal literature [e.g., Stock and Yogo, 2005, Andrews et al., 2019], but the connection is analogical rather than an application of weak-IV asymptotics. The model here does not introduce a weak instrument. The relevant empirical symptom is that the denominator based on residualised price variation can be small or highly design-dependent, making finite-sample centring and dispersion sensitive to the realised trajectory. We therefore use “limited identifying variation” as the primary description and reserve “weak identification” for the broader conceptual connection. 3

Variance components across units. To use multiple realised price histories, we adapt a standard random-effects variance-component estimator from meta-analysis [Paule and Mandel, 1982, DerSimonian and Laird, 1986, Hartung and Knapp, 2001]. The Paule–Mandel estimator is not a mathematical contribution of the paper. Its role is to estimate excess between-unit dispersion under a working model in which units provide approximately independent design realisations, within-unit variances are adequately measured, and the design-specific displacement is exchangeable with mean zero. When the true unit-level elasticities are common, this excess dispersion can be interpreted as design uncertainty under those assumptions. When true elasticities differ, the between-unit component generally combines genuine heterogeneity with design uncertainty, so it no longer identifies the latter without additional structure. Relation to pricing and inference practice. Limited and endogenous price variation is a long-standing problem in empirical demand estimation [Villas-Boas and Winer, 1999, Bijmolt et al., 2005], and recent pricing work emphasizes the value of controlled variation for learning demand and treatment heterogeneity [Ferreira et al., 2016, Dubé and Misra, 2023]. Our contribution is narrower: we use the simulation environment to distinguish additional rows observed under essentially the same price path from additional, weakly dependent price trajectories, and to quantify how that distinction affects repeated-design error. The centring issue is also related to bias-aware inference [Armstrong and Kolesár, 2020], although the displacement studied here is generated by the realised pricing design rather than by a generic smoothing-bias bound. Multiway clustering and related covariance corrections remain relevant for dependence within the observed panel [Cameron et al., 2011, Chiang et al., 2022]; they answer a different question from learning the distribution of errors across unrealised pricing designs. Scope of the evidence. Proposition 1 below is an algebraic variance identity. All quantitative magnitudes—including the 97.6% decomposition, the coverage results, the estimated exponent −0.271, and the variance-component performance—are simulation results from the stated DGP and grid. We do not interpret the exponent as a general rate, the baseline variance share as a population constant, or the failure of the eight evaluated intervals as an impossibility theorem. The simulations are intended to isolate a mechanism and to show conditions under which data design, rather than row count alone, materially changes inference.

2

Setup

2.1

The estimand

Let i index product units, r regions and t weeks. The outcome is Yirt = log Qirt , log volume; si , the log list price the manufacturer sets. We work with the the treatment is Tirt = log Pirt partially linear model [Robinson, 1988] Y = θ T + g(W ) + ε,

T = m(W ) + η,

E[ε | W, η] = 0, E[η | W ] = 0,

(1)

with W a vector of observed confounders (promotional flag and intensity, log competitor price, weather, holidays, working days, week of year, log inflation). The parameter θ is estimated with a cross-fitted residual-on-residual procedure motivated by Double Machine Learning [Chernozhukov et al., 2018]. Nuisance functions ℓ̂ = Ê[Y | W ] and m̂ = Ê[T | W ] are fit on 4

K = 5 contiguous temporal blocks, with all regional observations of a week assigned to the same block. The implementation aggregates fold-specific coefficients by their median, as in (2); because this is not the canonical pooled DML2 formula, all claims below should be read as applying to the estimator actually implemented here rather than to DML estimators as a class: P

i∈Ik T̃i Ỹi , 2 i∈Ik T̃i

θ̂ = median P k

Ỹi = Yi − ℓ̂(−k) (Wi ),

T̃i = Ti − m̂(−k) (Wi ).

(2)

Remark 1 (the estimand under split pricing). In the channel that motivates this work the manufacturer sets the list price while a shopkeeper sets the shelf price, so volume responds to a price the manufacturer does not control. Writing ρ = ∂ log P so /∂ log P si for the pass-through and εc for the consumer elasticity against the shelf price, the quantity identified by (2) is the convolution θ = εc ρ and not εc . Everything below concerns θ; the separation of the two is a distinct problem and is not our subject. We note the point only so that the ground truth against which we measure is unambiguous: it is εc ρ as realised in each generated panel, read from the generator rather than from its configuration.

2.2

The generator

Panels are drawn from a data-generating process described in Appendix A. Volume is generated jointly with prices, costs, promotions, calendar effects, weather and an inflation index, so that confounding is present by construction. The baseline configuration is W = 120 weeks, six regions, list prices moving ten times per series by 3.0–7.5%, pass-through ρ = 0.85, a cross-price elasticity of +0.30 on the log competitor price, and a demand shock of standard deviation 0.05 in logs. To ensure that this data-generating process reflects realistic market dynamics rather than a pathological edge case, these parameters are calibrated against the empirical moments in Nakamura and Steinsson [2008]. In US microdata, regular price changes exhibit a median monthly frequency of 9–12%—corresponding to 8–11 months of median duration, or roughly 2.5–3.3 price movements over a 120-week horizon. The median absolute size of regular price adjustments is 8.5%, whereas temporary sales are more than three times larger at a median of 29.5%. The baseline simulation regime directly mirrors these benchmark frequencies and magnitudes. A design is a realisation of everything except the demand shock; a replication of a design is a fresh draw of that shock alone. This separation is what makes Section 3 possible and is implemented by giving the shock its own random stream. Two learners recur throughout. gbr is a gradient-boosted regressor (depth 3, 200 trees, learning rate 0.05), the specification most common in applied DML. sieve is a ridge on an explicit basis: the confounders, a quadratic time trend and three annual harmonic pairs. They differ sharply in bias and variance, and the contrast turns out to matter for the aggregation result of Section 6.

3

Within- and between-design uncertainty

Definition 1 (within- and between-design error dispersion). Let D denote a design, u a shock realisation, and θ(D) the design-specific ground truth used by the generator. Define the 5

Table 1: Decomposition of the dispersion of the estimation error. Twelve designs, forty shock replications each (n = 480). σw is measured within design, σb is the standard deviation of the b is the weekly moving-block bootstrap standard design-specific conditional mean error b(D); se error from the baseline specification. Coverage is averaged over the design-specific conditional coverage probabilities and is measured against each design’s own ground truth, at a nominal 0.95. 2 +σ 2 ) b σb2 /(σw Learner Bias σw σb se Coverage b gbr sieve

0.150 0.016

0.0756 0.0589

0.4815 0.7187

0.1595 0.1553

97.6% 99.3%

0.565 0.242

estimation error e(D, u) = θ̂(D, u) − θ(D),

(3)

and its design-specific conditional mean b(D) = Eu [e(D, u) | D]. The within-design variance is 2 σw = ED [Varu (e(D, u) | D)] ,

(4)

and the between-design centring variance is σb2 = VarD (b(D)) .

(5)

2 VarD,u (e(D, u)) = σw + σb2 .

(6)

By the law of total variance, 2 + σ 2 + b̄2 . If b̄ = ED [b(D)] is nonzero, the corresponding mean-squared error is σw b

Definition 2 (conditional and repeated-design coverage). Let CI1−α (D, u) denote an interval computed from one realised panel. Its conditional coverage given D is Pr(θ(D) ∈ CI1−α (D, u) | D) .

(7)

u

Its repeated-design coverage under the simulation DGP is h

i

Pr (θ(D) ∈ CI1−α (D, u)) = ED Pr(θ(D) ∈ CI1−α (D, u) | D) . u

D,u

(8)

The equality is a probability identity; the substantive distinction is which source of randomness is treated as relevant to the inferential question. A within-panel procedure is constructed from one realised design. Depending on the resampling scheme and dependence structure, it may approximate aspects of the conditional distribution more or less well, but it does not by itself provide nonparametric information about the distribution of b(D) over price trajectories that were not realised. We therefore do not equate the bootstrap standard error mechanically with σw . Instead, we measure σw and σb directly from the generator. We draw 12 designs and 40 shock replications within each, estimate θ on all 480 panels, and compute the error decomposition relative to each design’s ground truth. Table 1 reports the result. Three features deserve comment. 6

Between-design centring dispersion is large in the baseline DGP. It accounts for 97.6% of the variance of the estimation error for gbr and 99.3% for sieve. Conditional on a design, the estimator is relatively concentrated—σw = 0.0756 for gbr—but its conditional mean error varies substantially across designs. These percentages characterize the simulated generator and should not be read as universal variance shares for short pricing panels. The bootstrap standard error is not an estimate of the full decomposition. For gbr, the mean bootstrap standard error, 0.1595, is about 2.1 times the measured within-design standard deviation and about one third of σb . Thus it is not accurate to describe this bootstrap as simply estimating σw in the finite sample considered here. The more limited conclusion is that a procedure built from one realised panel does not reproduce the across-design distribution measured by repeated generation of price trajectories. The simulations point to a centring component. The observed coverage shortfall is difficult to reconcile with interval width alone. For gbr, a typical half-width of about 0.305 is large relative to σw = 0.0756, yet mean conditional coverage across designs is 0.565. In the generator, the design-specific conditional mean error b(D) varies substantially across designs. A rough calculation based on the dispersion of b(D) yields coverage of the same order as the simulation. We interpret this as evidence that design-dependent centring is an important mechanism in this DGP, not as a proof that every resampling method fails whenever treatment variation is sparse. Remark 2 (which target is the right one). For a firm interpreting one realised historical trajectory, conditional coverage is a natural target. For evaluating a procedure that will be reused across future pricing histories, repeated-design coverage is also informative. Neither target dominates by definition; the relevant one depends on the decision problem. The simulations report both so that a conditional inferential question is not inadvertently replaced by an unconditional one.

4

No evaluated within-panel construction achieves nominal coverage

To assess whether familiar within-panel procedures are sufficient in this DGP, we compare eight constructions on identical fits over 200 independently drawn panels: the baseline moving-block bootstrap over weeks; the same at 600 draws; a hierarchical block bootstrap that also resamples cells within replicated weeks; the analytic i.i.d. standard error; cluster-robust by week; multiway cluster-robust by week and region [Cameron et al., 2011, Chiang et al., 2022]; a Newey–West long-run variance on the weekly score [Newey and West, 1987]; and a wild cluster bootstrap-t with Rademacher weights [Cameron et al., 2008]. None of the eight evaluated constructions reaches 0.95 coverage in this experiment (Table 2). Coverage is generally higher for wider intervals, and multiway clustering has the highest measured coverage for both learners among the procedures considered. This ranking should not be read as an impossibility result for all within-panel methods; it is a finite simulation comparison of these eight constructions. The table also emphasizes that the empirical shortfall is not resolved simply by choosing the widest evaluated interval. 7

Table 2: Eight interval constructions, identical point estimator and identical fits, over 200 panels. Nominal level 0.95. Reference repeated-design width is 3.92 σ̂ with σ̂ the realised across-panel standard deviation of the estimation error. This is a descriptive benchmark, not a confidence interval with a formal finite-sample coverage guarantee. gbr Construction Multiway cluster (week × region) Block bootstrap, cells resampled Newey–West on the weekly score Block bootstrap, B = 600 Block bootstrap, B = 250 (baseline) Wild cluster bootstrap-t Cluster-robust by week Analytic i.i.d. Reference repeated-design width 3.92 σ̂

sieve

Coverage

Width

Coverage

Width

0.730 0.595 0.580 0.545 0.525 0.350 0.345 0.285

1.062 0.712 0.798 0.591 0.597 0.451 0.445 0.338

0.660 0.435 0.230 0.300 0.310 0.105 0.105 0.155

1.167 0.723 0.451 0.581 0.566 0.258 0.254 0.308

1.680

2.212

For the decision exercise used in this paper, we pre-specify an application-specific width threshold of W ≤ 0.6. This threshold is not a general standard for pricing studies. Under that criterion, the higher-coverage intervals in Table 2 remain too wide to satisfy the paper’s operational precision requirement. The resulting coverage–width trade-off motivates the acrossunit variance-component exercise in Section 7.

5

An empirical dispersion pattern over the simulation grid

If design variance is what binds, the natural question is how much identifying variation would be needed to make it small. We sweep the number of price moves n ∈ {2, 4, 6, 8, 12, 16}, their magnitude (four ranges from 0.4–0.9% to 3.0–7.5%), the degree of confounding with promotion ({0, 0.5, 0.9}) and the pass-through ({0, 0.30, 0.60, 0.85}): 288 grid points, each estimated with both learners and replicated eight times, for 576 configurations and 4,608 fits in total. At each point we measure the realised dispersion of θ̂ across replications rather than its reported standard error. Let V = n · magnitude2 summarize the amount and size of list-price movement. The index is a deliberately simple design summary; it is not asserted to be Fisher information or a sufficient statistic for identification. Over the 24 points with no promotion confounding and full pass-through—six move counts × four magnitude ranges for learner gbr—a log–log regression gives σ̂b = 0.182 V −0.271 , s.e.(−0.271) = 0.023, R2 = 0.86. (9) Equation (9) is an empirical regularity of this simulation column. The exponent −0.271 should not be interpreted as a theoretical convergence rate for DML, for short panels, or for observational pricing designs in general. A −1/2 slope can serve as a heuristic reference in stylized settings where information grows proportionally with a sum of squared treatment movements, but V is not shown here to satisfy that information equivalence. The comparison is therefore descriptive rather than an asymptotic test. 8

Table 3: A selected column of the simulation grid: no confounding with promotion, ρ = 0.85, moves averaging 5.25%, learner gbr. True θ = −1.114; eight replications per grid point, so σ is itself estimated with visible noise — which is why the fit (9) is taken over the whole column rather than read off adjacent rows. Var(T̃ )/ Var(T ) is the share of the log list price surviving residualisation, i.e. the identifying variation the estimator actually uses. Filtered ratio indicates the proportion of simulated configurations satisfying the pre-estimation identification criterion (a treatment coefficient of variation CV > 0.03 and at least four discrete price movements). Moves

Bias

σ (design)

Var(T̃ )/ Var(T )

Filtered ratio

2 4 6 8 12 16

0.254 0.243 0.471 0.290 0.290 0.145

0.681 0.869 0.429 0.444 0.394 0.382

0.352 0.407 0.530 0.491 0.569 0.547

0.000 0.375 0.688 0.729 0.896 0.958

Within the simulated grid, larger V is associated with lower across-design dispersion, but the decline is slow enough that the explored configurations retain substantial error dispersion. Of the 576 learner–configuration combinations, none simultaneously attains absolute bias below 0.15 and design dispersion below 0.20. This is a statement about the enumerated grid and its finite replication count, not an impossibility result outside the grid. The best cells should likewise be interpreted cautiously because each grid point has only eight replications. Remark 3 (on extrapolating (9)). If one mechanically extrapolates the fitted relation, halving σb corresponds to multiplying V by approximately 21/0.271 ≈ 13. Such calculations extend beyond the simulated support and are included only to convey the curvature of the fitted relationship. They are not forecasts of how a real category would respond to thirteen times more price variation. Implication for precision calculations. On this grid, precision measures based on the reported within-panel standard errors can be much smaller than the realised repeated-design error dispersion. The median ratio of repeated-design dispersion to the reported standard-error scale is 2.26 for gbr and 8.03 for sieve. These ratios are simulation diagnostics, not generic correction factors for minimum detectable effects.

6

Common versus independent price paths under aggregation

The key distinction is not panel width by itself but the covariance structure of the design-specific estimation errors contributed by the added units. Proposition 1 (variance of averaged design-specific centring errors). Let bj be the design-specific P conditional mean error for unit j, and let b̄k = k −1 kj=1 bj . Then 



k X 1 X Var(b̄k ) = 2  Var(bj ) + 2 Cov(bj , bℓ ) . k j=1 j<ℓ

9

(10)

Table 4: Estimating the same object at three levels of aggregation, over 200 panels of eight product units in two brands of one category. Residualisation is always per unit. The Frisch– Waugh–Lovell logic [Lovell, 1963] relates the pooled residual-on-residual coefficient to a specification with unit effects; the exercise is designed so that aggregation combines information from multiple unit-specific price histories. Units is the number of units pooled per estimate. σ (design) is the dispersion across replications, and Width is the mean width of the baseline block-bootstrap interval at that level. Learner

Level

Units

Bias

σ (design)

RMSE

Coverage

Width

σ ratio

gbr gbr gbr

unit brand category

1 4 8

0.315 0.293 0.291

0.4603 0.2219 0.1538

0.559 0.368 0.327

0.474 0.370 0.280

0.693 0.414 0.364

— 2.07 2.99

sieve sieve sieve

unit brand category

1 4 8

0.021 0.021 0.022

0.4737 0.2267 0.1585

0.475 0.227 0.157

0.282 0.422 — 0.282 0.191 2.09 0.240 0.134 2.99 √ √ 4 = 2.00, 8 = 2.83

Predicted by Proposition 1 If Var(bj ) = σb2 and all pairwise correlations equal ρ, then

1 + (k − 1)ρ . (11) k √ Hence ρ = 0 gives a standard deviation of σb / k, while ρ = 1 gives no reduction. Aggregation does not remove a nonzero common mean bias E[bj ]. Var(b̄k ) = σb2

The proposition is an algebraic identity, not a claim that shared prices automatically imply ρ = 1 or that distinct price paths automatically imply ρ = 0. In the simulation, regions exposed to the same national list-price trajectory inherit a large common design component, whereas product units are generated with distinct price trajectories and approximately weak cross-unit dependence in that component. The empirical exercise below asks whether the observed covariance structure is close enough to the independent benchmark to produce the √ k pattern. Table 4 is close to the independent-design the observed √ benchmark in this simulation: √ reduction factors are 2.07 and 2.09 against 4 = 2.00, and 2.99 against 8 = 2.83, for both learners. This is evidence that the simulated cross-unit design-specific errors have low enough √ covariance for the k approximation to be useful here; it is not evidence that product-level price histories are independent in empirical applications. Two further readings of the table matter. First, aggregation improves RMSE substantially in the reported simulations, but the baseline interval does not gain coverage because its width contracts along with the empirical error dispersion. Second, the two learners respond differently. The gbr mean bias remains near 0.30 across aggregation levels, which is consistent with a persistent common centring component; its coverage falls as the interval tightens. The sieve mean bias remains near 0.02, so the reduction in weakly correlated dispersion translates more directly into lower RMSE. These are empirical patterns of the simulated portfolio, not generic properties of boosted trees or sieve learners. 10

Table 5: Six nuisance learners at unit level, 120 panels. Low-frequency share is the fraction of the residual’s spectral mass below one twentieth of the series length. No learner minimises bias, maximises coverage and minimises RMSE simultaneously. Learner

Bias

RMSE

Coverage

Low-frequency share

lasso ridge sieve rbf histgb gbr

−0.007 −0.008 −0.009 0.055 0.153 0.176

0.652 0.651 0.652 0.534 0.517 0.501

0.258 0.250 0.258 0.533 0.383 0.383

0.508 0.510 0.505 0.277 0.128 0.144

Table 5 places this in context. At unit level the choice of nuisance learner is a genuine trade-off: the regularised learners are nearly unbiased and have the worst RMSE and coverage, the boosted learners are the reverse, and no learner wins on all three. The ranking therefore changes with the aggregation level in these simulations. This illustrates, rather than proves generally, that nuisance-learner comparisons can depend on the level at which the estimand is reported, because aggregation attenuates weakly correlated dispersion but not a persistent common mean bias.

7

A variance-component interval estimated across realised designs

A single realised price trajectory does not nonparametrically identify the distribution of b(D) across counterfactual trajectories. Multiple units with independently or weakly dependently realised pricing designs can supply information about that distribution, but only under additional structure. We use the working model θ̂j = θj + Bj + εj ,

E[Bj ] = 0,

Var(Bj ) = τB2 ,

E[εj ] ≈ 0,

Var(εj ) ≈ s2j ,

(12)

with Bj exchangeable across units and approximately independent of the within-unit error εj . The interpretation of τB2 as design variance additionally requires that the units’ pricing trajectories act as independent or sufficiently weakly dependent design draws and that s2j adequately represents the within-unit component. Let θ̂j and s2j be the estimate and bootstrap variance of unit j, j = 1, . . . , J. We estimate an excess between-unit variance with the Paule–Mandel moment equation [Paule and Mandel, 1982] P 2 2 −1 X (θ̂j − µ̂)2 j (sj + τ ) θ̂j P = J − 1, µ̂ = (13) 2 + τ2 2 + τ 2 )−1 . s (s j j j j Paule–Mandel is a standard between-study variance estimator; the contribution here is its use as a working estimator of excess dispersion across independently realised pricing designs, not a new variance-component method. We compare the bootstrap percentile interval; a conjugate normal– normalqposterior interval based on a leave-one-out branch prior; q a variance-augmented interval post 2 2 θ̂j ± q sj + τ̂ ; and its posterior-centred analogue θ̂j ± q vjpost + τ̂ 2 , where q = z1−α/2 . 11

Table 6: Four intervals on identical fits, 200 panels of eight units per scenario (n = 1,600 unit-panels). Nominal level 0.95. In the homogeneous scenario the eight units share the same true θ, so τ̂ is interpretable as excess design-related dispersion under the working-model assumptions described in the text. Scenario

Interval

Homogeneous Homogeneous Homogeneous Homogeneous

Posterior-centred variance-augmented √ Variance-augmented s2 + τ̂ 2 Bootstrap√percentile Posterior v post

Heterogeneous Heterogeneous Heterogeneous Heterogeneous

Posterior-centred variance-augmented Variance-augmented Bootstrap percentile Posterior

√

v post + τ̂ 2

Coverage

Width

0.931 0.906 0.469 0.426

1.480 1.516 0.549 0.501

0.943 0.931 0.475 0.426

1.623 1.650 0.539 0.502

The homogeneous and heterogeneous scenarios have different interpretations. In the homogeneous scenario all eight units share the same true θ and have independently generated price paths. Under model (12), excess between-unit dispersion can then be attributed to the design component up to estimation error in s2j and τ̂ 2 . In the heterogeneous scenario the true θj differ, so the same between-unit component generally combines true effect heterogeneity and design-specific displacement. It should therefore be viewed as a conservative mixture rather than as a clean estimate of design variance. Table 6 reports the outcome. In the homogeneous scenario, adding the estimated betweenunit component raises empirical coverage from 0.469 for the bootstrap percentile interval to 0.931 for the posterior-centred variance-augmented interval. This is a substantial movement toward the nominal 0.95 level, but it is not exact nominal coverage. The estimated τ̂ = 0.372 is much larger than the mean bootstrap standard error of 0.144, which is consistent with substantial excess dispersion across independently generated unit-level designs in this simulation. Shrinkage alone does not address the simulated centring dispersion. The posterior interval has coverage 0.426, below the bootstrap percentile interval. In this DGP, shrinkage reduces the conditional variance while leaving design-specific displacement largely unmodelled. The result is consistent with the centring mechanism documented in Section 3; it should not be generalized to hierarchical Bayes procedures that explicitly model the design process or bias component. The coverage improvement is purchased with width. The two variance-augmented constructions are 2.70 and 2.76 times as wide as the bootstrap in the homogeneous simulation, at widths of 1.480 and 1.516. Under the paper’s pre-specified operational threshold, these intervals are too wide to support the intended unit-level pricing decision. The result illustrates the trade-off in this DGP: representing excess across-design dispersion improves coverage but can materially reduce decision precision.

12

√ Table 7: The variance-augmented interval θ̂ ± q s2 + τ̂ 2 at three levels of aggregation, 100 replications per scenario on a portfolio of 24 units √ (6 categories × 2 brands × 2 units). τ̂ is estimated between the units of each level, so its k column is the prediction of Proposition 1 applied to k = units pooled per estimate. Ratio to threshold indicates interval width expressed as a multiple of the 0.6 operational precision bound; no combination falls below 1.0. √ Scenario Learner Level k τ̂ k pred. Coverage Rel. Width (W/0.6) Homogeneous Homogeneous Homogeneous

gbr gbr gbr

unit brand category

1 2 4

0.4052 0.2779 0.1908

— 0.2865 0.2026

0.899 0.830 0.665

1.725 (2.88) 1.191 (1.99) 0.829 (1.38)

Homogeneous Homogeneous Homogeneous

sieve sieve sieve

unit brand category

1 2 4

0.4569 0.3104 0.2268

— 0.3231 0.2285

0.953 0.958 0.962

1.816 (3.03) 1.221 (2.04) 0.861 (1.43)

Heterogeneous Heterogeneous Heterogeneous

gbr gbr gbr

unit brand category

1 2 4

0.4471 0.3449 0.2850

— 0.3161 0.2236

0.938 0.930 0.893

1.877 (3.13) 1.432 (2.39) 1.166 (1.94)

Heterogeneous Heterogeneous Heterogeneous

sieve sieve sieve

unit brand category

1 2 4

0.5039 0.3832 0.3249

— 0.3563 0.2520

0.974 0.983 0.993

2.003 (3.34) 1.506 (2.51) 1.250 (2.08)

8

The variance-component interval at higher aggregation levels

Sections 6 and 7 suggest a natural√combined exercise. In the simulated portfolio, aggregation is close to the independent-design k benchmark, while the variance-component construction produces a wider interval at unit level. Combining them is therefore the natural question, and it is the one on which the practical value of the whole argument turns: does the variancecomponent interval, evaluated at a higher level of aggregation, become narrow enough to support a decision? Arithmetic from Tables 4 and 6 suggests it should. At category level the design dispersion is 0.1585 and the bootstrap standard error 0.034, so the variance-augmented interval would √ have width 2 × 1.96 × 0.0342 + 0.15852 = 0.636, against the 1.516 that the same construction attains at unit level in Table 6 — moving from uninformative toward the target precision bound. The arithmetic is not decisive, however, because τ̂ is re-estimated among the units of whatever level is being published, and its magnitude at that level is not the design dispersion of Table 4. We therefore run the construction directly, on a portfolio of 24 units — six categories, two brands each, two units per brand — estimating θ at each of the three levels and solving (13) between the units of that level: 24 units at unit level, 12 at brand, 6 at category, over 100 replications per scenario. For the evaluated portfolio and threshold, the result is negative (Table 7). Three readings are useful. Coverage remains near or above nominal for one learner in this experiment. sieve covers 0.953, 0.958 and 0.962 at the three levels of the homogeneous scenario, and 0.974 to 0.993 in the heterogeneous one. Its τ̂ declines close to the independent-design benchmark 13

(0.4569 → 0.3104 → 0.2268 versus 0.3231 and 0.2285), providing a second simulation check of the covariance pattern in Section 6. For gbr, the mean bias remains persistent as aggregation increases and coverage declines from 0.899 to 0.665 in the homogeneous scenario. In the heterogeneous scenario the decline is milder, while τ̂ also includes genuine effect heterogeneity. The width remains above the pre-specified threshold. The narrowest interval that covers at all is sieve at category level, 0.861, still 1.43 times the operational precision threshold. Of the twelve combinations none covers 0.90 within a width of 0.6; the closest approach in coverage, sieve at category level in the heterogeneous scenario, covers 0.993 at a width of 1.250. The arithmetic prediction of 0.636 was optimistic for the reason anticipated above: τ̂ among the six category-level units of this portfolio is 0.2268, not the 0.1585 design dispersion of Table 4, whose category aggregate pools eight units rather than four. In the heterogeneous scenario √ the interval is wider. With truths that differ across categories, τ̂ falls more slowly than k (0.5039 → 0.3832 → 0.3249 against 0.3563 and 0.2520), because part of the between-unit component is genuine heterogeneity rather than design error. The resulting interval has coverage 0.993 in the reported cell. Under the working model this is consistent with a conservative mixture of effect heterogeneity and design dispersion; it should not be interpreted as calibrated estimation of either component separately. √ Remark 4 (what would fit). Extrapolating the √ k rate from the homogeneous sieve row, and holding s ≈ 0.05, a width of 0.6 requires s2 + τ̂ 2 ≤ 0.153, hence τ̂ ≤ 0.145 and k ≈ (0.4569/0.145)2 ≈ 10 units with independently realised price paths per published estimate. This portfolio offers four. Whether an aggregate spanning roughly ten independently priced units remains aligned with the operational decision unit is application-specific. The extrapolation carries the caveat of Remark 3 — it extends an observed rate one doubling beyond the range measured. For the particular portfolio, learners, scenarios and width threshold studied here, no evaluated aggregation level simultaneously achieves the paper’s coverage and precision criteria. This motivates examining the assignment mechanism itself, while stopping short of an impossibility claim for other estimators, portfolios or data-generating processes.

9

Implications for data design

Adding rows is not equivalent to adding independent treatment variation. When all regions face the same national list-price path, additional regions can still reduce outcome noise, help estimate nuisance functions, and improve precision conditional on that path. What they do not provide is an additional independent realisation of the price trajectory. Proposition 1 makes the relevant distinction explicit: the gain from aggregation is governed by the covariance of design-specific errors, not by the raw number of rows. Longer panels help only through the variation they actually add. In the simulation grid, larger V = nmoves × magnitude2 is associated with lower across-design dispersion. If the fitted relation (9) were used descriptively, doubling V would be associated with a reduction in σb by a factor of about 20.271 = 1.21. Because the exponent is a simulation regularity and V is 14

only a heuristic index, this arithmetic should not be used as a general forecast for extending a real panel. Independent pricing paths can be more valuable than replicated exposure to one path. In the simulated portfolio, product units with separately generated price trajectories √ display an approximately k reduction in design-specific dispersion. The key empirical requirement is low covariance of the relevant design errors; distinct product labels alone do not guarantee it. In an application, the covariance of price-setting rules, common cost shocks and synchronized promotions would need to be assessed before treating product histories as independent design draws. Randomisation is one transparent way to create and justify independence. Controlled regional price assignment can generate treatment variation whose assignment mechanism is known, thereby supporting design-based reasoning in a way that passive histories generally cannot. Under the illustrative assumptions of Proposition 1, taking the baseline√ σb = 0.4815 and imposing independent, mean-zero regional design errors would imply 0.4815/ 30 ≈ 0.088 for an average across thirty regions. This is an algebraic illustration, not a simulated result for a thirty-region experiment. Natural experiments, staggered policy changes, or other sources of plausibly exogenous and weakly dependent price variation could play a similar identifying role. The central recommendation is therefore to create or exploit independent identifying variation, not that randomisation is the only admissible design.

10

Limitations

Synthetic evidence. Every quantitative result is measured on a generator written for this study. This is useful because repeated price trajectories and design-specific ground truth are observable by construction, but it sharply limits external validity. The simulations establish that the proposed mechanism can be quantitatively important under the stated DGP; they do not establish that between-design dispersion dominates for every short pricing panel or every estimator. The error decomposition must match the implemented ground truth. The formal decomposition in Section 3 is defined for e(D, u) = θ̂(D, u) − θ(D). This matters because the generator allows the design-specific truth to vary through pass-through. Any implementation that computes σb from VarD {Eu [θ̂ | D]} without subtracting θ(D) would combine variation in the estimand with variation in estimation error. Reproducibility code should therefore report explicitly which object is used in the decomposition. A heuristic variation index, not an information measure. The index V = nmoves × magnitude2 is a useful low-dimensional summary of the simulation grid, but the paper does not derive it as Fisher information or prove that estimator dispersion must scale as a power of V . Consequently, the fitted exponent −0.271 is a descriptive simulation coefficient and extrapolations from (9) are illustrative only.

15

Variance-component assumptions. Interpreting Paule–Mandel’s τ 2 as design variance requires approximately independent or weakly dependent design draws, adequate withinunit variance estimates, exchangeability of the design-specific displacement and, for a clean interpretation, common unit-level truths. When true elasticities vary, τ̂ 2 generally mixes genuine heterogeneity with design uncertainty. With only eight units in the main homogeneous exercise, uncertainty in τ̂ 2 itself can also be material. One estimator implementation. The simulations use the estimator in (2), including median aggregation of fold-specific residual-on-residual coefficients. This is DML-motivated but is not the canonical pooled DML2 estimator. The canonical DML theory also relies on regularity and dependence conditions that are not established here for the short serially dependent panel. The paper should therefore avoid attributing the simulation findings to Double Machine Learning as a class. Whether analogous between-design dispersion arises for instrumental-variable, structural, Bayesian, or alternative orthogonal-score estimators remains an empirical and theoretical question. Calibration and decision thresholds. The W ≤ 0.6 precision threshold is a pre-specified operational criterion for the simulation exercise, not a universal standard for pricing decisions. Likewise, the identification filter is calibrated on the same generator and has limited transportability across configurations. These thresholds are useful for organizing the experiment but should not be interpreted as externally validated cutoffs. External validation. A natural next step is to compute the proposed variation summaries and dependence diagnostics on real price histories, ideally in settings where multiple quasiindependent or randomized price paths exist. Such evidence would be needed before interpreting the simulation magnitudes as representative of empirical pricing panels.

11

Conclusion

This paper uses a synthetic pricing environment to separate two sources of inferential uncertainty that are easy to conflate in short panels. The first is variation conditional on one realised price trajectory. The second is variation in the estimator’s conditional mean error across alternative trajectories generated by the pricing process. In the baseline DGP, the second component is quantitatively large: for the gradient-boosted specification it accounts for 97.6% of the variance of the estimation error. The number is simulation-specific, but the decomposition clarifies why an interval based on one realised panel need not represent repeated-design performance. The simulation evidence also refines the diagnosis of undercoverage. The moving-block bootstrap standard error is not simply too small relative to within-design dispersion; in fact it exceeds the measured σw in the baseline decomposition. The more important feature is that the estimator’s conditional centre varies across realised price histories. None of the eight withinpanel constructions evaluated here reaches nominal coverage, although this finite comparison is not an impossibility theorem. The result motivates explicitly modelling or sampling the distribution of designs rather than treating a wider conventional standard error as a complete solution.

16

Two constructive findings follow. First, the gain from aggregation depends on the covariance of √ design-specific errors. Proposition 1 shows exactly why independent design draws produce a k reduction in standard deviation and why a common component limits that gain. The simulated product units are close to the independent benchmark, whereas additional exposure to a common price path does not create the same source of identifying variation. This is the precise sense in which adding observations is not equivalent to adding identification. Second, a standard between-unit variance component can be useful when multiple independently realised price paths are available. In the homogeneous simulation, the Paule– Mandel-based variance augmentation raises empirical coverage from 0.469 to 0.931 for the posterior-centred construction, at the cost of much wider intervals. This exercise does not establish a new meta-analytic estimator. It shows that, under a random-bias working model, information across designs can represent a component that a single realised trajectory cannot identify nonparametrically. When true unit effects differ, the between-unit component mixes heterogeneity with design uncertainty and must be interpreted more cautiously. The fitted relation σ̂b ≈ 0.182V −0.271 provides a compact summary of the simulation grid, not a scaling law. Its role is descriptive: within the explored DGP, substantially more independent price movement is associated with lower across-design dispersion, but the decline is slow over the observed range. The broader empirical lesson is therefore about data design. If the inferential target requires performance across plausible future price histories, collecting more rows under essentially the same treatment path may be less valuable than generating additional, credibly independent price variation. Controlled regional randomisation is one transparent way to create such variation; other quasi-experimental sources may serve the same purpose when their assignment and dependence structure are defensible. The paper’s contribution is consequently best read as a shift in emphasis from “which standard error should be attached to this one passive panel?” toward “what variation would make the elasticity identifiable and its uncertainty learnable at the decision level?” The simulations suggest that, in sparse pricing regimes, better inference and better data design are closely linked. Establishing how far that conclusion travels beyond the present generator is the next empirical task. Reproducibility. The generator, the estimators, the thirty-five experiments and the preregistered decision rules that produced every figure in this paper are published as an executable notebook. All results are obtained from synthetic data and no commercial information is used.

17

A

The data-generating process

The data generating process (DGP; Cadahia [2026]) produces a weekly panel at the unit × region × week level. Volume is drawn against the shelf price, which is generated from the list price at a pass-through rate that may be constant, heterogeneous across regions, or dependent on the shopkeeper’s margin state. Prices, promotions, competitor prices, costs, weather, holidays and an inflation index are generated jointly so that confounding is present by construction. The demand shock is drawn from a dedicated random stream, which is what allows a design to be held fixed while the shock is resampled (Section 3). All monetary quantities are expressed relative to a reference list price p0 ; the panel starts on 2 January 2023 and runs W Mondays.

A.1

Exogenous series

For week t = 0, . . . , W − 1 the inflation index is It = 100 (1.0016)t (1 + νt ) with νt ∼ N (0, 0.0022 ); holidays per month and working days (22 minus holidays) come from a fixed calendar map; naP tional real income is Stnac = 100 (1.0015)t and its regional counterpart is Srt = Stnac exp( s≤t ζrs ) with ζrs ∼ N (0, σS2 ), which is what gives the cash-pressure index a regional component. Weather is climart = Tr + 6 sin(2π woyt /52 − 1.2) + N (0, 1), with Tr ∼ U (13, 31) drawn once per region. Variable cost starts at 0.50p0 and receives four step shocks of ±(2–6)% p0 at random weeks, clipped to [0.30, 0.62] p0 .

A.2

Prices, promotions and the competitor

Promotions are 6 to 10 windows of 2–3 weeks per series; the flag is promort ∈ {0, 1} and the intensity is pintrt = πir promort , where πir ∼ U (0.10, 0.25) is drawn once per series, so a promoted week is discounted by the same amount throughout a series. The list price is a step function,   P si Pirt = clip p0 + k≤t δirk , 0.72p0 , 1.55p0 , (14) where nmoves weeks are drawn without replacement from [6, W − 4] and each contributes a jump δ = ±U (mag) p0 with a random sign. Two switches control the confounding of the treatment. With promo_conf = 0 a move that falls on a promotion week is discarded, so price and promotion are orthogonal by construction; with promo_conf > 0 the move is relocated onto a promotion week with that probability, which is how the confounded regime is produced. In the collinear regime the list price is replaced by p0 (Crt /1.05p0 )0.95 , a near-deterministic function of the competitor’s price. The competitor’s price is a random walk around 1.05p0 with weekly standard deviation 0.004p0 , plus comp_moves discrete jumps of ±U (4%, 9%) p0 ; when κ = comp_react > 0 it also
P si follows the own price with one week’s lag, C ← C exp κ ∆ log P , and the result is s≤t s−1 clipped to [0.70, 1.45] p0 . Without discrete jumps the competitor’s log price has a standard deviation of about 1.5% over 120 weeks, below the demand shock, and the cross-price channel is not identified by construction; this is why comp_moves = 8 in every experiment run on this generator.

18

A.3

Pass-through and the shelf price

The shopkeeper’s price is so Pirt

= 1.12 p0

si Pirt p0

!ρirt

1 − 0.6 pintrt ,

(15)

with a pass-through that is heterogeneous across regions and dependent on the retailer’s margin state, 



ρirt = clip ρ̄ir 1 + λ

m∗ − Mir,t−1 , 0, 1.2 , m∗ 



ρ̄ir = clip(ρi mr , 0, 1),

(16)

so si )/P so ∗ where Mir,t−1 = (Pir,t−1 − Pirt ir,t−1 is the retailer’s margin carried into the week, m = 0.12 2 is the target margin, mr = clip(1 + N (0, σρ ), 0.25, 1.6) is drawn once per region, and λ governs the state dependence: when the margin falls below target the shopkeeper transmits more. In the round-point regime the shelf price is pinned, P so = 1.12p0 (1 − 0.6 pint), so ρ = 0 and the list price does not enter demand at all. Because (16) makes ρ a function of the realised series, ρi is not the estimand. The generator therefore computes the realised pass-through of each series, so , log(P si /p ) Cov log P̃irt irt 0
= , si Var log(Pirt /p0 )

ρeff ir

P̃ so =

P so , 1.12p0 (1 − 0.6 pint)

(17)

and stores it in the panel. The ground truth against which every table in this paper measures is θi = βi ρ̄eff i , read from the generated panel rather than from its configuration; comparing against βi or against the configured ρi would report generator dispersion as estimator bias.

A.4

Demand

Sell-out volume is so Pirt Crt + 0.30 log + 0.40 promort 1.12p0 1.05p0 It + 0.05 cprt + uirt , + 0.05 (climart − Tr ) + 0.10 log 100

log Qso irt = log 1000 + βit log

(18)

with uirt ∼ N (0, σu2 ) and cprt a cash-pressure index built as a fortnightly calendar term minus standardised log regional income. The elasticity profile βit is constant unless a structural break (t∗ , β post ) is injected. When an asymmetry a is requested the level term is replaced by a Houck P decomposition in the first differences of log(P so /1.12p0 ): β(1 − a) s≤t (∆ log Psso )+ + β(1 + P a) s≤t (∆ log Psso )− . Sell-in volume adds forward buying and, optionally, order refusal: Qsi = Qso (1 + firt ) + N (0, 0.022 ) Qso , where f = 0.30 in the two weeks preceding each list-price rise above 2%. Note that (15) and (18) together imply ∂ log Q/∂ log P si = βρ, which is the convolution discussed in Remark 1. Nominal and deflated prices. The panel stores prices in nominal terms, multiplied by It /100, while demand (18) is generated against the deflated series. The estimator’s treatment is therefore the nominal log list price, and log inflation is among the controls W , so the deflation cancels in the partialled-out regression; we record the asymmetry because it is the kind of detail that decides whether a replication reproduces a bias of 0.15 or of 0.20. 19

Table 8: Baseline configuration. Every table in this paper is generated at the baseline except in the column indicated; entries marked not reported here belong to experiments of the same run whose results this paper does not use. Symbol

Meaning

Baseline

Varied in

W R p0 nmoves mag ρi σρ λ promo_conf comp_moves κ cross σu σS a

weeks regions reference list price list-price moves per series move magnitude configured pass-through regional dispersion of ρ state dependence of ρ confounding of moves with promotion competitor discrete moves competitor reaction to own price cross-price elasticity demand shock, logs regional income dispersion injected asymmetry

120 6 5,200 10 3.0–7.5% 0.85 0 0 0 8 0.5 +0.30 0.05 0.020 0

— 8–30, not reported here — {2, 4, 6, 8, 12, 16}, §5 four ranges, §5 {0, 0.30, 0.60, 0.85}, §5 0.10–0.18, not reported here 0.35–0.45, not reported here {0, 0.5, 0.9}, §5 — 0 in Tables 4, 6, 7 — — — 0.25, not reported here

Seed separation. Two independent generators of randomness are used. The design stream draws prices, promotions, the competitor, costs, weather, income and the regional pass-through multipliers; the shock stream draws uirt and the sell-in noise. Fixing the first and varying the second resamples the demand shock while holding the design fixed, which is the mechanism of Section 3. All other experiments vary both.

A.5

Regimes, portfolio and baseline parameters

A regime is a configuration of the price-generating block: clean (nmoves = 10, magnitude 3.0– 7.5%, no confounding), weak (2 moves of 0.4–0.9%), confounded (as clean but promo_conf = 0.9), collinear (list price following the competitor at 0.95), and round point (as clean but with the shelf price pinned, so θ = 0). The default portfolio has eight units in four brands and two categories, with consumer elasticities from −0.90 to −1.40 and configured pass-through from 0 to 0.85, spanning the five regimes. Experiments that need a controlled topology substitute their own portfolio: Section 6 uses eight clean units in two brands of one category (β = −1.30 and −1.00), Section 7 eight clean units sharing one brand, and Section 8 six categories × two brands × two units, all clean. The second generator. The cross-generator check of Section 10 uses the data-generating process of the baseline data pipeline, written earlier and independently. Its structure is the same — (15) and (18) with a constant pass-through of 0.85 — but its topology is fixed: six units across three brands covering the five regimes, six named regions with fixed mean temperatures, and no state-dependent pass-through, no regional income component and no discrete competitor moves. It is the generator behind the recovery experiment; the extended one described above is used everywhere else.

20

B

Estimators and replication counts

B.1

Nuisance learners and inference

The confounder set is: W = {promotional flag, promotional intensity, log competitor price, weather, holidays in the month, working days, week of year, log inflation}. gbr is a gradient-boosted regressor (maximum depth 3, 200 trees, learning rate 0.05, subsample 0.8) on those columns plus a week index. sieve is a cross-validated ridge (penalty selected over 25 values on a log grid from 10−3 to 103 ) on a standardised explicit basis: the confounders, a standardised week trend and its square, and three annual harmonic pairs in the week of year. The remaining learners of Table 5 share the sieve basis (ridge at a fixed penalty, lasso at α = 0.001, rbf a Nyström feature map followed by cross-validated ridge) or the tree family (histgb, histogram gradient boosting, depth 3, 250 iterations, learning rate 0.06). Nuisance functions are fit on K = 5 contiguous temporal blocks with all regional observations of a week assigned to the same block, and with no embargo between blocks. The latter is a known limitation: a week can be split between training and test through another region. An embargoed variant is implemented and measured, and is not adopted here because it would change the residualiser that two of the ablations compare. The point estimator is the median across folds, (2). The choice is supported for the boosted learner and not for the sieve: over 200 panels the paired contrast in absolute error against the pooled aggregate is −0.0911 (s.e. 0.0152, t = −6.0) for gbr, in favour of the median, and +0.0400 (s.e. 0.0099, t = 4.0) for sieve, against it. Against the across-fold mean the median wins for gbr (−0.1974, t = −10.2) and ties for sieve (+0.0108, t = 1.0). We report the median throughout and record that at the aggregation levels of Section 8 the aggregate estimator is the pooled one, since a fold median is not defined across stacked units. Block length for the moving-block bootstrap is b = clip(round(1.5 W 1/3 ), 2, ⌊W/3⌋), giving b = 7 at W = 120; blocks are drawn over weeks and every regional observation of a resampled week travels with it, except in the hierarchical variant of Table 2, which additionally resamples cells within each replicated week.

B.2

Replication counts

Table 9 reports the experiments behind each table of the paper. Replications are independent panels; a unit-panel is one estimated unit × replication pair, which is the quantity that determines the standard error of a coverage figure. The full run comprises 35 experiments and 69.5 hours of aggregate compute; the remaining 24 experiments concern components of the broader decision framework that this paper does not report. Seed separation. Selection and reporting use disjoint seeds. The bench that chose among interval constructions and learners ran on seeds 20,000–24,000 and the audit that verified the pre-registered rules on 30,000–34,000, while the runs reported here use bases outside both ranges: 1,000–16,000 for the experiments inherited from the pipeline and 40,000–59,000 for those introduced in this paper. A published figure therefore does not inherit the selection bias of having chosen the best of several variants on the same draws. 21

Table 9: Replication counts of the experiments reported in the paper. Seconds are aggregate compute over the replications of the experiment, executed on eight cores. Where two scenarios are run the count is reported as replications × scenarios. Table

Experiment

1 2 3 4 5 6 7

cobertura_condicional inferencia_variantes frontera nivel_identificacion aprendiz_matriz jerarquia_cobertura jerarquia_nivel

App. B §10 §10 §10

estimador_puntual recovery recovery_ext calib_vs_eval

Reps

Unit-panels

Seconds

12 × 40 200 8 200 120 200 × 2 100 × 2

480 200 2,304 2,200 120 3,200 8,400

2,475 3,164 10,573 7,877 1,092 14,818 36,525

200 500 150 60

200 500 150 240

1,134 38,903 8,683 1,172

Pre-registered verdicts. Every claim in this paper corresponds to a rule written before the run, with its threshold fixed in advance, and each rule returns pass or fail on the measured quantity. Of 30 rules, 13 pass, 16 fail and one does not apply because the failure it was written to diagnose did not reproduce. These outcomes form the empirical core of Sections 4–8: the claim that the baseline interval achieves nominal coverage, the claim that some within-panel construction covers, the claim that the shortfall is purely one of width, the claim that target coverage is obtained at a practical width, the claim that a single learner dominates across bias, coverage, and error, and the claim that the variance-component interval meets the precision threshold at some level of aggregation, all fall short of their pre-registered criteria.

22

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