Beyond IPS: Reliable Counterfactual Evaluation in Multi-Stage Ad Systems without Logged Propensities

Introduction

Offline evaluation of ranking models is a critical safeguard in large-scale advertising and recommendation systems, where deploying a poorly performing model can degrade user experience and business outcomes. The industry invests heavily in developing complex deep neural network (DNN) based ranking models, but before any new policy is launched, it must be rigorously assessed using historical production logs to ensure reliability and safety Yi et al. [ [22]. More broadly, offline evaluation plays two complementary roles in modern ad systems. First, it acts as a risk mitigation mechanism by identifying problematic models before they are exposed to real user traffic. Second, it serves as a scaling factor for online experimentation: large-scale ad systems typically have limited A/B testing capacity, making it infeasible to evaluate many candidate model changes online at once. Offline evaluation therefore provides a high-throughput filtering stage, allowing practitioners to prioritize the most promising policies for scarce online experimentation resources [17, 16].

Accurate offline evaluation in modern advertising systems is fundamentally challenging due to the complexity of the underlying data generating process. In modern ad platforms, exposure is determined by a multi-stage pipeline that combines multiple ranking models and platform policies including auctions, filtering, and business rules rather than a single stochastic ranking policy [3, 9]. Consequently, the observed data reflects a time-varying mixture of production policies [2]. Action propensities are typically neither logged nor well-defined, rendering inverse propensity based estimators inapplicable in practice [22, 21, 7].

Predictive metrics such as log-loss, AUROC, and Relative Information Gain (RIG) measure accuracy on logged data but do not estimate the value of the actions a new policy would take [9, 5, 22]. Counterfactual evaluation estimates this value on historical contexts [24], either by reweighting logged data with inverse propensity scoring (IPS), its self-normalized variants [3], and doubly robust (DR) estimators [6], including extensions to deterministic logging and low overlap [21, 12], or by simulation and direct replay with learned response models [2, 8, 11]. IPS-style estimators require logged propensities, which unlogged post-ranking system operations in multi-stage ad systems (e.g., caching, audience targeting) make unavailable, while simulation and replay must predict outcomes for actions that were never logged, often where overlap with the logs is limited [4, 12].

To address these limitations, recent work has focused on reward modeling approaches that learn a predictive model of user response from logged data, and use it to estimate the value of new policies by replaying them on historical contexts [24, 10, 20]. When the distribution of counterfactual actions under a target policy differs substantially from the distribution induced by the logging mixture, domain shift can make reward predictions unreliable on the actions that matter for evaluation. In this case, a reward model trained on logged data may exhibit systematic misprediction on target-policy actions and produce biased policy value estimates [12].

In this paper, we develop a reward-modeling framework for offline counterfactual evaluation under policy-induced distribution shift, and analyze its reliability theoretically and empirically. Our contributions are:

(1) Mixture-weighted reward model training without propensities. We introduce a practical method for direct-method counterfactual evaluation under multi-stage delivery: a single reward model trained to be accurate across a set of candidate policies by reweighting the supervised loss with mixture-induced density ratios estimated

(2) Reliability of replay Direct Method. We derive a value error bound that holds with high probability for the Direct Method estimator used in our experiments. The bound separates reward model error where the logging data provide support, error from impressions with limited overlap, and error due to a finite evaluation sample. It makes explicit the finite-sample tradeoff between reward model error on well-supported impressions and error from impressions with limited logging support. Under consistency, only the error from impressions with little or no logging support remains asymptotically, motivating a rule for deciding when offline evaluation is sufficient and when online A/B testing is needed.

(3) Empirical evaluation on synthetic and production data. We benchmark six estimators on a configurable ads simulator and on production traffic from a large-scale CTR ranking system, and show that the mixture-weighted reward model improves policy selection over its unweighted counterpart in both settings, with the largest gains at low overlap.

Literature Review

A substantial body of applied research evaluates ad ranking and click-through prediction models using predictive metrics computed over logged impressions, such as log-loss, AUROC, AUC-lift, and NDCG. These approaches have powered large-scale ad systems. Examples include Facebook’s logistic-regression and feature-engineering pipeline [9], the adoption of deep architectures such as Wide & Deep for CTR estimation [5], and multi-task models such as ESMM that jointly learn click and conversion probabilities on display-ad traffic [15]. While effective at measuring predictive performance under the production exposure distribution, such offline metrics do not capture a model’s counterfactual effect on ad delivery, user experience, or revenue. This motivates the need for counterfactual and causal evaluation methods that estimate what would happen if a new ranking model were deployed.

A natural alternative to predictive metrics is off-policy evaluation (OPE), which estimates the value of a new ranking policy using data logged under a different policy. Classical OPE methods include IPS and its self-normalized variants [3], doubly robust estimators [Dudík et al., 2011], and model-based or direct-method approaches [20], as well as more recent advances addressing deterministic logging and low-overlap regimes [21, 12]. Propensity-based methods provide unbiased or partially identified estimates when key assumptions hold: the logged propensities must be known, the target policy must have support under the logging policy, and no unobserved transformations may occur between action selection and outcome. In multi-stage ad systems, these conditions are violated because downstream post-ranking system operations (e.g., auctions, audience targeting and business rules) transform the ranking model’s output in ways that are unlogged, nonlinear, and not recoverable from impression logs. Consequently, OPE estimators cannot identify the true value of a ranking model, limiting their reliability for offline evaluation.

A complementary line of work seeks to evaluate or optimize ad systems via simulation, typically by replaying historical auctions and combining logged data with predictive models. Early systems at Bing combined web-scale Bayesian CTR models with auction replay to study policy changes [8]. Later work formalized this idea as auction-based offline evaluation: Yi et al. [ [22] proposed simulated metrics by rerunning sponsored-search auctions offline and estimating user responses from historic clicks; Bottou et al. [ [3] discussed counterfactual ad-placement evaluation via a predictor that runs the auction and a click model trained offline; Bayir et al. [ [2] introduced an “open box” counterfactual policy estimator for optimizing sponsored-search marketplaces; and Bai et al. [ [1] built an auction simulation system to optimize constrained mechanism parameters on an e-commerce platform. Li et al. [ [14] frames large-scale sponsored-search auctions as explicitly multi-objective, optimizing tradeoffs among platform, advertiser, and user objectives via an online optimization formulation. More recently, open-source and industrial simulators such as AuctionGym [11] and Uber’s ads simulation framework [23] provide environments for testing bidding and allocation strategies under synthetic or replayed traffic. These approaches are powerful when the auction logic and downstream system operations are fully specified and stable, so that the simulator achieves high fidelity to production behavior.

Approach

Problem Setup

Let $x \in\mathcal{X}$ denote a context (user features) and let $a \in\mathcal{A}(x)$ denote an action (ad selection) available in context $x$. A (ranking) policy $\pi$ is a deterministic mapping from contexts to actions: $\pi(x)$ denotes the action selected by $\pi$ on context $x$. We call the pair $z=(x,a)$ an impression, write $\mathcal{Z}=\{(x,a):x \in\mathcal{X}, a \in\mathcal{A}(x)\}$ for the impression space, and let $r^{\star}(z)$ denote the unknown expected reward (e.g., click probability). We assume rewards are bounded: $r^{\star}(z) \in[0,R_{\max}]$ for all $z \in\mathcal{Z}$ and we take $R_{\max}=1$ throughout, as our rewards are click probabilities in CTR prediction. Each policy $\pi_j$ induces a distribution $\mathcal{P}_{\pi_j}$ on $\mathcal{Z}$; we write $\operatorname{supp}(\mathcal{P}_{\pi_j})$ for the set of impressions that $\pi_j$ produces with positive density. We observe $n$ logged impressions

collected under a production logging policy $\pi_0$, where $r_i$ is the realized reward for impression $z_i$. Let $P_X$ denote the marginal distribution over contexts in $\mathcal{D}$.

We wish to evaluate $N$ candidate policies $\pi_1,\ldots,\pi_N$ using only the logged data $\mathcal{D}$. Each candidate policy $\pi_j$ may select a different action $\pi_j(x)$ on the same context, inducing a different distribution over impressions $\mathcal{P}_{\pi_j}$. The value of policy $\pi_j$ is the expected reward under its induced impressions,

In particular, $V_0$ is the value of the current production (logging) policy. Our analysis assumes that each candidate policy can be replayed on the logged contexts and that the reward distribution for a given impression is unchanged between the logging and candidate-policy distributions. In practice, only a small number of candidate policies can be validated through online A/B testing due to limited experimentation capacity, making it critical to select the best policy among $N$ candidates using offline estimates. Our goal is therefore not only to estimate $V_j$ accurately, but to do so well enough to reliably rank the candidates and minimize the regret of selecting a suboptimal policy for deployment in these limited A/B testing slots.

Direct Method based Approach

Deterministic logging, missing propensities, and unobserved multi-stage system transformations make propensity-based estimators (e.g., IPS and its variants) difficult to apply reliably. We therefore resort to the Direct Method (DM) [6, 20, 2]: for each candidate $\pi_j$, we learn a reward model $\hat{r}$ from logged data, apply $\pi_j$ to each logged context $x$, and estimate the value as

In practice, over a held-out evaluation split $\mathcal{D}_{\mathrm{eval}} \subset\mathcal{D}$ of size $m = \lvert\mathcal{D}_{\mathrm{eval}}\rvert$, we use the empirical replay mean $\hat{V}^{\mathrm{DM}}_j = m^{-1}\sum_{(z_i,r_i)\in\mathcal{D}_{\mathrm{eval}}}\hat{r}(x_i,\pi_j(x_i))$, which is the estimator used in our experiments. The key limitation of DM is policy-induced distribution shift: $\hat{r}$ is trained on impressions from $P_{\pi_0}$ but evaluated on impressions from $P_{\pi_j}$, which can differ substantially [18, 19]. When $\hat{r}$ is inaccurate where $P_{\pi_j}$ places mass but $P_{\pi_0}$ does not, $\hat{V}_j$ is biased; if this bias differs across candidates, it can distort their ranking and lead to selecting a suboptimal policy.

Mixture-Weighted Reward Model Training

To correct the policy-induced distribution shift between the logging data and the candidate policies, we replay all $N$ candidates on the logged contexts and train a single shared reward model whose loss is weighted to target a mixture of the candidate-policy distributions, rather than the logging distribution alone. The target mixture distribution over impressions is

where the coefficients $\beta_1,\ldots,\beta_N$ encode how strongly each candidate distribution is emphasized during training. Under no prior information about which candidates are more important, the natural default is uniform weighting: $\beta_j = 1/N$, which we use throughout. Let $p_0(z)$ and $p_j(z)$ denote the density functions of $P_{\pi_0}$ and $P_{\pi_j}$, respectively, and define the mixture density $p_{\mathrm{mix}}(z) \triangleq\sum_{j=1}^{N}\beta_j p_j(z)$.

On the region where $p_0(z) > 0$, define the per-impression mixture-to-logging density ratio and the per-policy density ratios:

We call $\Omega_j(z)$ the true per-policy density ratio of candidate $\pi_j$ to the logging policy, and $\Omega(z)$ the mixture ratio, which serves as a per-impression importance weight: it up-weights logged impressions that are likely under the candidate policies and down-weights those that are only relevant to the logging policy.

Let $\mathcal{F}$ denote the reward-model class, let $f \in\mathcal{F}$ be a candidate reward predictor, and let $\ell$ be a per-sample loss with realized reward $Y$. Using the density ratio $\Omega(z)$, define the mixture-weighted risk

The learned reward model is denoted by $\hat{r} \in\mathcal{F}$. Equation (6) targets the candidate-mixture risk restricted to the support of the logging distribution. In practice, $\Omega(z)$ is unknown and must be estimated from data, as described in § 3.4.

Estimating Density Ratios via Domain Classification

The per-policy density ratios $p_j(z)/p_0(z)$ in (5) cannot be computed directly, since neither the logging nor the candidate distributions have known density functions. We estimate them by training a multiclass domain classifier that learns to distinguish which policy generated a given impression [19]. We construct a replay dataset in which the logging class is represented by the actual logged impressions and each candidate class by replayed counterfactual actions on the same contexts. Counterfactual candidate actions $\pi_j(x_i)$ are produced by shadow-mode scoring in the production experiment and by offline replay of the candidate’s scoring function on the logged contexts in simulation. Each impression is paired with a label $g \in\{0,1,\ldots,N\}$ indicating its generating policy ($g=0$ for the logging policy, $g=j$ for candidate $\pi_j$). We then train a domain classifier $q_\theta(g \mid z)$ to predict the policy label from the impression, using any architecture that outputs a probability distribution over the $N+1$ labels, with standard multiclass cross-entropy and uniform class priors.

Under equal class priors, the standard density-ratio identity [19] gives

Replacing the population posterior $q^*$ with the learned classifier $q_\theta$ gives the estimated per-policy ratios below; substituting these estimates into (5) gives the estimated mixture weight:

where $\widehat{\Omega}_j(z)$ is the estimated per-policy density ratio of candidate $\pi_j$ to the logging policy.

The estimated weights $\widehat{\Omega}(z)$ can have heavy tails when $q_\theta(0 \mid z)$ is small, i.e., when the classifier is confident that an impression was not generated by the logging policy. To prevent a few extreme weights from dominating the training loss, we clip $\widehat{\Omega}(z)$ to a maximum value $c$:

We monitor the effective sample size [13] (ESS) as a diagnostic for weight concentration:

In our experiments, we report ESS/$n$, which lies in $[1/n,1]$. When ESS/$n \approx1$, the weights are roughly uniform and the logging and candidate distributions overlap well. When ESS/$n \ll1$, a few impressions dominate the weighted loss, signaling poor overlap and potential instability in the value estimates. The reliability of the estimated weights, and therefore of ESS as an overlap diagnostic, depends on whether the impression representation preserves policy-induced differences and whether the domain classifier produces reliable probabilities. We return to this issue empirically in Appendix § 14.

Value Estimation Error Decomposition

To understand when mixture-weighted training improves policy ranking and when it cannot, we bound the value estimation error by the sum of three terms: an overlap error, a cold-start term, and a replay concentration term. Definition 3.1 partitions the impressions produced by each candidate policy according to whether the logging policy provides high or low density there, with $\tau$ controlling a trade-off between the resulting error terms.

The terms are as follows. Let $w(z)\equiv\Omega(z)$ denote the true mixture-to-logging density-ratio weight, let $\widetilde{w}(z)\equiv\widehat{\Omega}(z)$ denote its unclipped domain-classifier estimate, and define $\widetilde{w}(z)\equiv\widetilde{\Omega}(z)=\min\{\widehat{w}(z),W\}$, where $W=c$ is the clipping threshold from (10). Define the corresponding population risks

Let

denote the best predictor in the model class under the true weighted population risk. Define the logging-distribution overlap error by

Here, $\mathcal{O}_j(\tau)$ is the overlap region defined in Equation (7). $A_{\mathcal{F}}=R_w(f_{\mathcal{F}}^\star)-R_w(r^\star)$ is model-class approximation error (best-in-class weighted risk minus the Bayes risk). $\epsilon_{\mathrm{opt}}$ is the optimization error defined in Assumption A3. $\Gamma_{n_{\mathrm{tr}}}(\delta_{\mathrm{tr}})$ is a high-probability $(1-\delta_{\mathrm{tr}})$ bound on the weighted uniform deviation $\sup_{f\in\mathcal{F}}|\widetilde{R}_w(f)-\widehat{R}_w(f)|$ (generalization) for the clipped-weighted loss class. Define

and

Thus $\epsilon_w$ combines domain-classifier ratio-estimation error and clipping bias. $\mu_j(\tau)=P_{\pi_j}(\mathcal{C}_j(\tau))$ is the cold-start mass on the region $\mathcal{C}_j(\tau)$ defined in Equation (7); the computable $q_\theta$ plug-in requires a classifier calibration or error correction. Finally, $\beta_j$ is the candidate mixture share, $P_{\mathrm{mix}}=\sum_j\beta_jP_{\pi_j}$; $c_\ell$ is the calibration constant (1 for squared loss and 1/2 for log loss); and $m$ is the number of replay contexts.

The full proof is given in Appendix § 9.

Corollary 3.5 shows that the regret of offline policy selection is controlled by the worst-case value estimation error across candidate policies. In particular, uniformly accurate value estimates guarantee reliable policy selection; large errors for either the optimal policy or the selected policy can directly translate into suboptimal deployment decisions. The proof is a straightforward triangle-inequality argument and is deferred to Appendix § 10.

Corollary 3.6 is a population asymptotic routing rule, applicable when the reducible model-fit, weighted-generalization, weight, and replay finite-sample terms in Theorem 3.3 are negligible. Its $q_\theta$-based implementation additionally requires classifier calibration/error control. For finite samples, the routing decision must use the full value-error bound in Theorem 3.3. The proof of Corollary 3.6 is given in Appendix § 11.

Synthetic Data Experiments

Simulation Environment and Setup

We developed a custom simulation framework for offline ranking policy evaluation. The simulator maintains a fixed corpus of users and ads, each represented as a feature vector, and an oracle reward function that captures nonlinear user-ad interactions to assign an expected reward to any (user, ad) pair. Each logged impression consists of a randomly drawn user presented with $k$ candidate ads; the acting policy scores each candidate and selects the highest-scoring ad, and the oracle evaluates the resulting (user, ad) pair to produce a reward. We use 10,000 users, 1,000 ads, and $k=10$ candidates per impression, with 70,000 logged impressions per trial split into four disjoint folds: 20,000 for domain-classifier training, 20,000 for reward-model training, 10,000 for calibration, and 20,000 for evaluation. Unless otherwise noted, reward models are trained for 30 epochs, domain classifiers for 4 epochs, estimated weights are clipped at $c=100$, and results are aggregated over 50 seeds. We publicly release the simulator and synthetic evaluation code.² The simulator provides full observability: exact ground-truth policy values are obtained by applying each candidate to the held-out evaluation contexts and querying the oracle. Each candidate policy scores (user, ad) pairs the same way as the logging policy but with shifted scoring parameters. A calibration sweep over these shifts places the candidates of a trial at value multipliers $V_j/V_0 \in\{0.95, 1.00, \ldots, 1.20\}$ and at a common target ESS of their true density ratios relative to the logging policy, one of $0.25, 0.35, \ldots, 0.85$; if no shift reaches a candidate’s value target, that candidate is omitted. Full details of feature distributions, oracle reward function, logging-policy construction, and the calibration sweep are in Appendix § 8.

Estimators

We evaluate six estimators in the synthetic experiments. Let $\{(z_i,r_i)\}_{i=1}^{m}$ denote the logged impressions in the evaluation split, $\hat{r}(z)$ a learned reward model, and $\hat{\Omega}_j(z)$ the estimated per-policy density-ratio weight from the multiclass domain classifier of § 3.4. Define its clipped version as $\tilde{\Omega}_j(z) \triangleq\min\{\hat{\Omega}_j(z),c\}$. (i) IPS: importance-weighted average of logged rewards, $\hat{V}^{\mathrm{IPS}}_j = (1/m)\sum_i \tilde{\Omega}_j(z_i)r_i$. Since true propensities are unavailable, IPS uses the same classifier-based density-ratio estimates as the weighted DM and doubly robust (DR) estimators. (ii) Unweighted DM: the standard direct method with $\hat{r}$ trained on the logging distribution under uniform sample weights and replayed on candidate-policy actions. (iii) Weighted DM (ours): the mixture-weighted reward model from Section 3.3, trained with the clipped mixture weight $\tilde{\Omega}_j(z)$ from (10) and replayed on candidate-policy actions. (iv) Per-policy Weighted DM: $N$ separately trained reward models, with model $j$ trained using $\hat{\Omega}_j(z)$; it uses the same data splits, architecture, optimizer, epochs, calibration, and clipping settings as Weighted DM. (v) Unweighted DR: the doubly robust method using the unweighted reward model plus the residual correction $(1/m)\sum_i \hat{\Omega}_j(z_i)(r_i-\hat{r}(z_i))$. (vi) Weighted DR (ours): the same residual correction using the mixture-weighted reward model as the control variate.

Evaluation Metrics

In each trial, we evaluate $N$ candidate target policies $\pi_1,\ldots,\pi_N$. Let $V_j \triangleq V(\pi_j)$ denote the oracle value of $\pi_j$, and let $\hat{V}_j$ denote the policy-value estimate produced by each method. We report the following metrics. Top-1 regret (Reg). Let $\hat{j} \triangleq\arg\max_j \hat{V}_j$ be the deployed policy choice and $j^\star\triangleq\arg\max_j V_j$ the oracle-best. Top-1 regret is $V_{j^\star}-V_{\hat{j}}$ averaged over trials: the value lost by deploying the offline-selected policy instead of the true best. For Per-policy Weighted DM, whose $N$ reward models each produce their own estimate $\hat{V}^{(j)}_0$ of the logging-policy value, $\hat{j}$ maximizes the estimated improvement $\hat{V}_j-\hat{V}^{(j)}_0$. Top-1 accuracy (Acc). $\mathbb{I}\{\hat{j}=j^\star\}$ averaged over trials: the fraction of trials in which the correct policy is selected. Value MAE% (MAE%). $\frac{100}{N}\sum_{j=1}^{N}|\hat{V}_j-V_j|/V_j$: the mean absolute percentage error of the estimated policy values $\hat{V}_j$ against the oracle values $V_j$, averaged over the $N$ candidate policies in a trial.

Experiment 1: Estimator Comparison Under Distribution Shift

We compare the six estimators of § 4.2 across the seven ESS targets of § 4.1. With 50 seeds per target, this gives 350 trials, grouped into three regimes by ESS target (Table 1). The regime headers in Table 1 report the corresponding mean cold-start mass at $\tau= 0.1$, linking the empirical ESS grouping to the overlap diagnostic in the value-error bound.

Method	Acc$\uparrow$	Reg$\downarrow$	MAE$\% \downarrow$	Acc$\uparrow$	Reg$\downarrow$	MAE$\% \downarrow$	Acc$\uparrow$	Reg$\downarrow$	MAE$\% \downarrow$
IPS	0.60	0.0041	7.64	0.65	0.0045	5.49	0.71	0.0028	4.15
Unweighted DM	0.67	0.0044	7.20	0.87	0.0006	2.58	0.96	0.0003	1.59
Weighted DM (ours)	0.81	0.0014	2.65	0.91	0.0004	1.94	0.98	0.0000	1.86
Per-policy Weighted DM	0.75	0.0028	3.61	0.83	0.0013	2.80	0.90	0.0006	2.32
Unweighted DR	0.82	0.0016	2.64	0.93	0.0002	0.70	1.00	0.0000	0.30
Weighted DR (ours)	0.90	0.0005	1.71	0.95	0.0001	0.43	0.99	0.0000	0.21

Table 1 reports performance across the three ESS regimes. The IPS baseline ranges from 0.60 to 0.71 Top-1 accuracy across regimes. Mixture weighting clearly helps: Weighted DM improves over Unweighted DM on eight of nine regime-metric comparisons, and it outperforms Per-policy Weighted DM on all nine, so its gains cannot be explained by candidate-specific reweighting alone. Weighted DR is best on all three metrics in the Low and Mid regimes; in the High regime, Unweighted DR has slightly higher Top-1 accuracy, the two DR estimators tie on regret, and Weighted DR has lower Value MAE%. Full per-bin breakdowns with standard errors and the per-policy Value MAE% breakdown are in Appendix § 12. To test sensitivity to the clip $c$ in Equation (10), which trades off removing the up-weighting that corrects the shift (small $c$) against letting a few impressions dominate the training loss (large $c$), we repeat the Experiment 1 setup with $c \in\{1, 5, 10, 20, 100\}$; the results are in Appendix § 13. At every overlap level, Value MAE% is nearly the same for $c \in\{10, 20, 100\}$, a range that includes the $c = 100$ used in Experiment 1. In contrast, $c = 1$, which removes all up-weighting, stays close to the unweighted model at low overlap and is best only at high overlap.

Production Data Experiment

Setup. We evaluate production traffic from a large-scale industrial CTR ranking system with one production logging policy and five candidate treatment policies. Each of the six policies served a separate share of live production traffic in an online A/B test, so its true value $V_j$ is the observed click-through rate on the evaluation impressions it served. Top-1 accuracy is computed over the five candidates, so random selection gives an accuracy of $1/5 = 0.20$. Value MAE% averages over all six policies, including the logging policy. All metrics are averaged over 50 random subsamples of the production data, with estimated weights clipped at $c = 20$. Weighted DM and Per-policy Weighted DM use the same data splits, architectures, optimization, calibration, and clipping settings.

Results. Among the DM estimators in Table 2, Weighted DM performs best on all three metrics. Relative to the Per-policy Weighted DM baseline, it improves Top-1 accuracy from 0.24 to 0.40, reduces regret from 0.00676 to 0.00244, and reduces Value MAE% from 12.43 to 11.56. It also outperforms Unweighted DM, which obtains 0.36 Top-1 accuracy, 0.00271 regret, and a Value MAE% of 14.10. Per-policy Weighted DM reweights toward each candidate with its own reward model, so the gain of Weighted DM cannot be explained by per-candidate reweighting or by training more reward models.

Method	Acc$\uparrow$	Reg$\downarrow$	MAE%$\downarrow$
IPS	0.24	0.00807	4.14
Unweighted DM	0.36	0.00271	14.10
Weighted DM (ours)	0.40	0.00244	11.56
Per-policy Weighted DM	0.24	0.00676	12.43
Unweighted DR	0.38	0.00225	1.90
Weighted DR (ours)	0.44	0.00226	2.04

Among the DR estimators, Weighted DR achieves the highest Top-1 accuracy, while Unweighted DR has marginally lower regret and Value MAE%, so neither DR variant dominates. IPS and both DR estimators attain much lower Value MAE% than all DM estimators (1.90–4.14 versus 11.56–14.10), but IPS has the highest regret (0.00807) and ties Per-policy Weighted DM for the lowest Top-1 accuracy (0.24). The production candidates are nearly tied: Weighted DM’s estimated winner exceeds the runner-up by only 0.15% on average (descriptive paired-bootstrap 95% interval [−0.31%, 0.60%]), and their ordering reverses in 24 of the 50 subsamples, so offline evaluation cannot reliably separate the top two candidates, and this candidate set should be sent to online A/B testing. Per-policy Value MAE% for each estimator is in Appendix § 15.

Conclusions

We studied offline evaluation of ad-ranking policies in multi-stage production pipelines, where logged propensities are unavailable and direct-method (DM) replay with learned reward models is often the only viable option. We proposed mixture-weighted reward modeling, which trains the reward model on logged data reweighted toward a mixture of candidate-policy distributions using density ratios estimated by a multiclass domain classifier. We bounded each candidate’s replay-DM value error by an overlap term, a cold-start term, and a replay concentration term, and derived an asymptotic rule that uses the cold-start term to decide, for a given regret budget, whether to trust the offline selection or route the candidates to online A/B testing.

In both the synthetic and production experiments, training a single reward model toward the candidate mixture makes DM replay more reliable under policy-induced shift: it improves policy selection most where overlap is weakest, and with a doubly robust correction it gives the highest Top-1 accuracy at low and medium overlap and on production data. The analysis also identifies the error that more logged data does not reduce: the bound retains a term for impressions a candidate generates where the logging data provide no support, and the cold-start mass bounds their share. Offline evaluation in multi-stage ad systems should therefore pair mixture-weighted reward models with an overlap diagnostic, trusting offline selection where overlap is adequate and reserving online A/B tests for candidates with large cold-start mass.

Limitations. Our analysis assumes candidate policies can be replayed on logged contexts and that an impression’s reward distribution does not depend on the policy that produced it. The cold-start mass is defined by the population domain posterior; computing it with the learned classifier requires calibration or error correction, and the weights are useful only when the representation retains policy-induced differences (Appendix § 14). The routing rule is asymptotic, and its operational performance under live traffic is left to future work. It also assumes that the weight error $\varepsilon_w$ vanishes, which, with a fixed clip $c$, requires the mixture ratio $\Omega(z)$ never to exceed $c$.

Acknowledgments and Disclosure of Funding

This work was funded by Meta Platforms, Inc. All authors are employees of Meta Platforms, Inc.

Synthetic Simulator Details

This appendix gives the simulator design used in Section 4: the user and ad features, the oracle reward function, the logging- and candidate-policy parameterization, and the per-trial pipeline.

Users, ads, and impression generation

The simulator maintains a fixed corpus of 10,000 users and 1,000 ads, each represented by a feature vector drawn i.i.d. uniformly from $[-1,1]^3$. Each logged impression is generated as follows: a user is sampled uniformly at random from the corpus, $k = 10$ candidate ads are sampled uniformly at random with replacement from the ad corpus, the acting policy scores each (user, ad) pair, and the highest-scoring ad is selected. The reward of an impression is the oracle’s expected reward for the resulting (user, ad) pair, without Bernoulli sampling. Each trial uses 70,000 impressions generated in this fashion.

Oracle reward function

The oracle is a sum of 400 Gaussian kernels in the joint user–ad feature space, each the product of a kernel on the user features and a kernel on the ad features, truncated at 1:

Here $x,a \in[-1,1]^3$ are the user and ad feature vectors. The kernel centers $\mu_\ell^x,\mu_\ell^a$ are drawn uniformly within $\pm0.5$ of the origin in each coordinate, widths $\sigma_\ell^x,\sigma_\ell^a$ uniformly from $[0.3, 0.5]$, and amplitudes $\alpha_\ell$ uniformly from $[0.2, 1.0]$, then rescaled so that the average reward of users paired with uniformly random ads is 0.15. The oracle is redrawn with each random seed, so all candidate policies in a trial are scored against the same ground truth. The oracle value $V_j$ of a policy $\pi_j$ is obtained by applying $\pi_j$ to the evaluation contexts and averaging the oracle reward of the ads it selects.

Logging policy and candidate-policy parameterization

The logging policy $\pi_0$ and the candidate policies $\pi_1,\ldots,\pi_6$ score a (user, ad) pair with a sum of 200 Gaussian kernels of the same product form as the oracle’s (Appendix § 8.2), whose centers lie within $\pm0.3$ of a policy center in each coordinate, with widths drawn uniformly from $[0.3, 0.5]$ and amplitudes from $[0.1, 1.0]$. The logging-policy center is drawn uniformly from $[-0.5, 0.5]^6$ for each seed. Candidate centers are positioned by a calibration sweep over a grid of offsets along the line from the oracle center (the origin) to the logging-policy center and along a random orthogonal direction. For each grid point, the sweep computes the value multiplier $V_j/V_0$ and the ESS of the true density ratio relative to $\pi_0$, computed from the kernel scores, on 10,000 logged impressions. For each of the six target multipliers $v_k \in\{0.95, 1.00, 1.05, 1.10, 1.15, 1.20\}$ and each of the seven ESS targets $\{0.25, 0.35,\ldots,0.85\}$, a grid point whose multiplier is within 0.03 of $v_k$ (or within 0.06 if none is) and whose ESS is closest to the target is selected, and the candidate is built at those offsets with its own random orthogonal direction and kernel draw. If no grid point qualifies, the candidate is omitted; as a result, 56 of the 350 trials evaluate fewer than six candidates.

Per-trial procedure

Each trial follows the same pipeline:

(1) Data collection and split. 70,000 logged impressions are collected under $\pi_0$ and partitioned into four disjoint folds: 20,000 for domain-classifier training, 20,000 for reward-model training, 10,000 for calibration, and 20,000 for evaluation.

(2) Domain classifier training and calibration. Each candidate policy $\pi_j$ is replayed on the contexts of the domain-classifier fold to produce counterfactual impressions; these, together with that fold’s logged impressions, form a multiclass dataset labeled by the generating policy. A one-hidden-layer MLP with 64 units is trained on this dataset with Adam (learning rate 0.01, batch size 512) for 4 epochs and calibrated by temperature scaling fitted on 5-fold out-of-fold predictions.

(3) Importance weights. The calibrated classifier is applied to the reward-model fold, and its outputs are converted to the clipped mixture weight $\widetilde{\Omega}(z)$, with uniform $\beta_j = 1/N$, and the clipped per-policy weights $\widetilde{\Omega}_j(z)$, using $c = 100$. Value MAE% is nearly the same for $c \in\{10, 20, 100\}$, a range that includes this $c = 100$ (Appendix § 13).

(4) Reward model training. The unweighted, mixture-weighted, and per-policy weighted reward models share the same architecture, a one-hidden-layer MLP with 64 units, and are trained on the reward-model fold with Adam (learning rate $10^{-3}$, batch size 512) for 30 epochs under a weighted log loss. They differ only in the sample weights: uniform, $\widetilde{\Omega}(z)$, or $\widetilde{\Omega}_j(z)$. Each model is temperature-calibrated on the calibration fold.

(5) Evaluation. On the evaluation fold, we compute the six estimators of § 4.2 for each candidate policy, with IPS and DR using the clipped per-policy weights $\widetilde{\Omega}_j$ of the evaluation fold’s logged impressions. Oracle values $V_j$ are obtained by applying each policy to the evaluation contexts and querying the oracle. The three metrics of § 4.3 are computed for each estimator. All training runs use a CPU.

Proof of Theorem 3.3: Replay-DM Value Estimation Error

Proof. Write $e(z) = \widehat{r}(z) - r^{*}(z)$.

Replay decomposition. Since $Z = (X, \pi_j(X))$ with $X \sim P_X$ has distribution $P_{\pi_j}$ (§ 3.1), Equation (2) gives $V_j = \mathbb{E}_{P_{\pi_j}}[r^{*}(Z)]$. Adding and subtracting the population replay mean $\mathbb{E}_{P_{\pi_j}}[\widehat{r}(Z)]$ gives

and the triangle inequality yields

Because $\widehat{r}$ is trained only on the training folds, it is a fixed function once we condition on them. By Assumption A4, the replay contexts $X_1,\ldots,X_m$ are i.i.d. from $P_X$ and independent of those folds, so the summands $\widehat{r}(X_s,\pi_j(X_s))$ are i.i.d. with mean $\mathbb{E}_{P_{\pi_j}}[\widehat{r}(Z)]$ and lie in $[0,R_{\max}]$ by Assumption A1. Hoeffding’s inequality followed by a union bound over the $N$ candidates therefore gives, with probability at least $1-\delta_{\mathrm{ev}}$,

simultaneously for all $j$. Splitting the population bias over the regions in Equation (7) yields

where the second inequality uses $|e(z)| \le R_{\max}$ from Assumption A1. Combining Equations (24)–(26) proves Equation (13).

Change-of-measure bound (i). For $z \in\mathcal{O}_j(\tau)$, Definition 3.1 implies

so $p_0(z) \ge\tau p_j(z)$ and hence $p_j(z)/p_0(z) \le1/\tau$. Therefore,

which is bound (i) in Equation (14).

Mixture-weighted bound (ii). Because $P_{\mathrm{mix}} = \sum_{k=1}^{N} \beta_k P_{\pi_k}$ with $\beta_j > 0$, its density satisfies $p_{\mathrm{mix}}(z) \ge\beta_j p_j(z)$. Cauchy–Schwarz and the fact that $\mathcal{O}_j(\tau)$ lies on logging support give

The last inequality applies the calibration condition of Assumption A2; the identification with weighted excess risk uses the shared conditional reward law given $Z$ and the support-restricted mixture identity in Equation (6).

It remains to control the weighted excess risk. Let $f_{\mathcal{F}}^\star$ be the best-in-class predictor from Equation (16). Adding and subtracting the clipped-weight population and empirical risks gives

On the training event, the second and fourth terms are each at most $\Gamma_{n_{\mathrm{tr}}}(\delta_{\mathrm{tr}})$ in absolute value, while Assumption A3 bounds the middle empirical-risk difference by $\varepsilon_{\mathrm{opt}}$. For any $f \in\mathcal{F}$,

Applying this inequality to the first and fifth terms of Equation (29), then adding the approximation error $A_{\mathcal{F}}=R_w(f_{\mathcal{F}}^\star)-R_w(r^\star)$, gives

Substituting Equation (31) into Equation (28) and taking square roots proves bound (ii) in Equation (14).

Joint probability. The weighted-risk bound holds on the training event with probability at least $1-\delta_{\mathrm{tr}}$, and the simultaneous replay bound holds with probability at least $1-\delta_{\mathrm{ev}}$. A final union bound gives joint probability at least $1-\delta_{\mathrm{tr}}-\delta_{\mathrm{ev}}$, completing the proof.

Proof of Corollary 3.5: Top-1 Selection Regret

Proof. By definition of $\hat j$, we have $\widehat V^{\mathrm{DM}}_{\hat j}\ge\widehat V^{\mathrm{DM}}_{j^\star}$. We decompose the regret as

The middle term is non-positive since $\widehat V^{\mathrm{DM}}_{\hat j}\ge\widehat V^{\mathrm{DM}}_{j^\star}$, and the remaining terms can be bounded using absolute values:

Finally, each term is bounded by the maximum estimation error across all policies, yielding

Proof of Corollary 3.6: Asymptotic Offline-vs-A/B Routing Rule

Proof. Write $\delta_{\mathrm{tr}}=\delta_{\mathrm{tr}}(n_{\mathrm{tr}})$ and $\delta_{\mathrm{ev}}=\delta_{\mathrm{ev}}(m)$, and let $B_j$ denote the right-hand side of form (ii) in Equation (14),

By Theorem 3.3, with probability at least $1-\delta_{\mathrm{tr}}-\delta_{\mathrm{ev}}$, simultaneously for all candidates $j$,

On the same event, Corollary 3.5 gives

where

Because $N$ and $\beta_1,\ldots,\beta_N>0$ are fixed, the assumed limits $A_F\to0$, $\epsilon_{\mathrm{opt}}\to0$, $\Gamma_{n_{\mathrm{tr}}}(\delta_{\mathrm{tr}})\to0$, and $\epsilon_w\to0$ give $\max_j B_j\to0$ in probability, and $\log(2N/\delta_{\mathrm{ev}})/m\to0$ sends the replay term to zero, so $\rho\to0$ in probability. Hence, for every $\eta>0$,

which is Equation (22). Finally, if Equation (23) holds, then $\{\operatorname{Regret}>\Delta+\eta\}\subseteq\{\operatorname{Regret}>2R_{\max}\max_j\mu_j(\tau)+\eta\}$, so $\Pr(\operatorname{Regret}>\Delta+\eta)\to0$.

Detailed Per-ESS-Bin Results for Experiment 1

This appendix breaks down Experiment 1 by the realized ESS, the ESS of the estimated mixture weights (Equation (11)), whereas Table 1 groups trials by ESS target: Top-1 accuracy (Table 3), Top-1 regret (Table 4), and Value MAE% (Table 5). We additionally report a per-policy Value MAE% breakdown by candidate value multiplier $v_k$ (Table 6). We include the same six estimators from § 4.2: IPS, Unweighted DM, Weighted DM, Per-policy Weighted DM, Unweighted DR, and Weighted DR. Each row of Table 3–Table 5 reports the mean $\pm$ standard error (SE $=$ std$/\sqrt{n}$) over trials assigned to the corresponding realized-ESS bin. The rounded bin labels from 0.1 through 1.0 are all populated across the 350 trials. Within each row, the best method mean is shown in bold.

ESS	$n$	IPS	Unweighted DM	Weighted DM (ours)	Per-policy Weighted DM	Unweighted DR	Weighted DR (ours)
0.1	22	$0.500 \pm0.107$	$0.409 \pm0.105$	$0.727 \pm0.095$	$0.818 \pm0.082$	$0.727 \pm0.095$	$0.773 \pm0.089$
0.2	26	$0.615 \pm0.095$	$0.654 \pm0.093$	$0.808 \pm0.077$	$0.692 \pm0.091$	$0.923 \pm0.052$	$0.962 \pm0.038$
0.3	35	$0.657 \pm0.080$	$0.600 \pm0.083$	$0.714 \pm0.076$	$0.714 \pm0.076$	$0.743 \pm0.074$	$0.857 \pm0.059$
0.4	26	$0.577 \pm0.097$	$0.769 \pm0.083$	$0.808 \pm0.077$	$0.846 \pm0.071$	$0.885 \pm0.063$	$0.885 \pm0.063$
0.5	30	$0.567 \pm0.090$	$0.900 \pm0.055$	$0.933 \pm0.046$	$0.667 \pm0.086$	$0.933 \pm0.046$	$1.000 \pm0.000$
0.6	34	$0.618 \pm0.083$	$0.882 \pm0.055$	$0.882 \pm0.055$	$0.824 \pm0.065$	$0.882 \pm0.055$	$0.971 \pm0.029$
0.7	50	$0.680 \pm0.066$	$0.920 \pm0.038$	$0.980 \pm0.020$	$0.860 \pm0.049$	$0.960 \pm0.028$	$0.960 \pm0.028$
0.8	41	$0.659 \pm0.074$	$1.000 \pm0.000$	$1.000 \pm0.000$	$0.902 \pm0.046$	$1.000 \pm0.000$	$1.000 \pm0.000$
0.9	71	$0.775 \pm0.050$	$0.944 \pm0.027$	$0.972 \pm0.020$	$0.901 \pm0.035$	$1.000 \pm0.000$	$0.986 \pm0.014$
1.0	15	$0.600 \pm0.126$	$1.000 \pm0.000$	$1.000 \pm0.000$	$0.933 \pm0.064$	$1.000 \pm0.000$	$1.000 \pm0.000$

ESS	$n$	IPS	Unweighted DM	Weighted DM (ours)	Per-policy Weighted DM	Unweighted DR	Weighted DR (ours)
0.1	22	0.0041 ± 0.0018	0.0094 ± 0.0026	0.0034 ± 0.0016	0.0048 ± 0.0024	0.0042 ± 0.0023	0.0012 ± 0.0006
0.2	26	0.0054 ± 0.0019	0.0048 ± 0.0017	0.0015 ± 0.0007	0.0023 ± 0.0012	0.0010 ± 0.0007	0.0005 ± 0.0005
0.3	35	0.0042 ± 0.0016	0.0035 ± 0.0015	0.0013 ± 0.0005	0.0026 ± 0.0012	0.0012 ± 0.0004	0.0005 ± 0.0002
0.4	26	0.0032 ± 0.0011	0.0012 ± 0.0006	0.0004 ± 0.0003	0.0008 ± 0.0005	0.0002 ± 0.0001	0.0002 ± 0.0001
0.5	30	0.0054 ± 0.0016	0.0004 ± 0.0003	0.0004 ± 0.0003	0.0028 ± 0.0010	0.0003 ± 0.0002	0.0000 ± 0.0000
0.6	34	0.0040 ± 0.0013	0.0004 ± 0.0003	0.0002 ± 0.0001	0.0018 ± 0.0009	0.0002 ± 0.0001	0.0000 ± 0.0000
0.7	50	0.0035 ± 0.0013	0.0003 ± 0.0002	0.0000 ± 0.0000	0.0008 ± 0.0004	0.0001 ± 0.0000	0.0001 ± 0.0000
0.8	41	0.0048 ± 0.0016	0.0000 ± 0.0000	0.0000 ± 0.0000	0.0006 ± 0.0003	0.0000 ± 0.0000	0.0000 ± 0.0000
0.9	71	0.0025 ± 0.0007	0.0004 ± 0.0003	0.0000 ± 0.0000	0.0005 ± 0.0002	0.0000 ± 0.0000	0.0000 ± 0.0000
1.0	15	0.0045 ± 0.0021	0.0000 ± 0.0000	0.0000 ± 0.0000	0.0002 ± 0.0002	0.0000 ± 0.0000	0.0000 ± 0.0000

ESS	$n$	IPS	Unweighted DM	Weighted DM (ours)	Per-policy Weighted DM	Unweighted DR	Weighted DR (ours)
0.1	22	8.14 ± 0.63	12.22 ± 1.32	3.62 ± 0.46	3.91 ± 0.50	5.26 ± 0.82	3.45 ± 0.54
0.2	26	7.25 ± 0.36	8.47 ± 0.89	2.70 ± 0.20	3.40 ± 0.42	2.88 ± 0.35	1.75 ± 0.24
0.3	35	6.95 ± 0.50	5.93 ± 0.51	2.40 ± 0.18	3.42 ± 0.34	1.75 ± 0.18	1.19 ± 0.10
0.4	26	7.04 ± 0.53	3.87 ± 0.39	1.61 ± 0.16	2.56 ± 0.24	1.17 ± 0.17	0.59 ± 0.07
0.5	30	5.28 ± 0.40	2.82 ± 0.28	2.17 ± 0.17	3.24 ± 0.30	0.80 ± 0.10	0.62 ± 0.06
0.6	34	6.23 ± 0.43	2.45 ± 0.24	1.64 ± 0.14	2.75 ± 0.23	0.73 ± 0.07	0.40 ± 0.04
0.7	50	5.85 ± 0.32	1.88 ± 0.15	1.92 ± 0.13	2.74 ± 0.19	0.54 ± 0.04	0.36 ± 0.03
0.8	41	4.54 ± 0.29	1.44 ± 0.12	1.79 ± 0.12	2.42 ± 0.15	0.38 ± 0.04	0.24 ± 0.02
0.9	71	4.10 ± 0.21	1.67 ± 0.09	2.07 ± 0.10	2.69 ± 0.10	0.30 ± 0.02	0.22 ± 0.01
1.0	15	4.59 ± 0.45	1.98 ± 0.26	1.92 ± 0.18	2.30 ± 0.22	0.23 ± 0.02	0.19 ± 0.01

$v_k$	$n$	IPS	Unweighted DM	Weighted DM (ours)	Per-policy Weighted DM	Unweighted DR	Weighted DR (ours)
0.95	350	5.11 ± 0.23	3.90 ± 0.33	2.13 ± 0.09	3.37 ± 0.12	1.18 ± 0.16	0.74 ± 0.09
1.00	350	5.44 ± 0.25	3.52 ± 0.25	2.04 ± 0.08	3.31 ± 0.14	1.02 ± 0.09	0.66 ± 0.06
1.05	350	5.32 ± 0.23	3.93 ± 0.29	2.02 ± 0.09	3.23 ± 0.13	1.21 ± 0.13	0.81 ± 0.09
1.10	343	6.42 ± 0.27	3.92 ± 0.32	2.24 ± 0.09	2.86 ± 0.13	1.36 ± 0.18	0.81 ± 0.10
1.15	336	6.13 ± 0.25	3.11 ± 0.22	2.22 ± 0.08	2.53 ± 0.12	0.98 ± 0.09	0.65 ± 0.06
1.20	294	5.62 ± 0.28	3.67 ± 0.28	2.32 ± 0.10	2.26 ± 0.11	1.20 ± 0.13	0.78 ± 0.08

Across realized-ESS bins, Weighted DR has the lowest Value MAE% in every row, decreasing overall from 3.45 at ESS 0.1 to 0.19 at ESS 1.0. It also has the lowest regret in the three lowest-ESS bins, while multiple reward-model estimators reach near-zero regret as overlap increases. Top-1 accuracy improves overall with overlap, although the leading estimator varies by bin: Per-policy Weighted DM is strongest at ESS 0.1, Weighted DR leads at ESS 0.2, 0.3, 0.5, and 0.6, and Weighted DM leads at ESS 0.7. The per-policy breakdown shows that Weighted DR has the lowest Value MAE% for every candidate value multiplier, while Weighted DM improves on Unweighted DM for all six candidates.

Synthetic Experiment 2: Sensitivity to Importance Weight Clipping

A practical question for any density-ratio weighting scheme is how aggressively to clip the estimated weights. Clipping truncates the upper tail of the density-ratio weights, attenuating the correction for impressions far from the logging distribution; at $c = 1$ all un-weighting is removed. We study this tradeoff across different levels of policy-logging overlap, using the same simulation setup as Experiment 1.

Because policies are kernel scoring functions in the same feature space, the true mixture density ratio $\Omega(z) = p_{\mathrm{mix}}(z)/p_0(z)$ can be computed analytically from kernel scores, without a domain classifier. We use the ESS of these kernel-based weights as the ground-truth overlap measure, decoupling it from both the domain classifier and the clip threshold. We run 50 seeds × 7 ESS levels, each evaluated at $c \in\{1, 5, 10, 20, 100\}$; the same domain classifier is trained once per trial and the five clip values are applied post hoc.

Figure 1 shows that Value MAE% is largely insensitive to the clip threshold for $c \in\{10, 20, 100\}$: in every kernel-ESS bin these three settings differ by at most 0.52 percentage points, while at kernel ESS 0.2–0.4 they reduce Value MAE% by 4.1–8.2 points relative to the unweighted model. From kernel ESS 0.5 upward, $c = 5$ matches or slightly improves on these settings, but at kernel ESS 0.2–0.4 its Value MAE% is higher (e.g., 3.20 versus 2.10–2.62 at kernel ESS 0.3). The exception is $c = 1$: at kernel ESS 0.3–0.4 its Value MAE% (6.24–6.55) is close to that of the unweighted model (6.69–7.27), whereas at kernel ESS 0.9–1.0 it attains the lowest Value MAE% (1.54 and 1.38, versus 1.90–2.36 for the unweighted model and the other clip values). In Top-1 regret and accuracy, $c = 1$ is likewise closest to the unweighted model at kernel ESS 0.3–0.4; at kernel ESS 0.2, $c = 5$ and $c = 20$ have Top-1 regret 0.0137 versus 0.0036 for the other clip values. The clip value used in Experiment 1, $c = 100$, lies in this insensitive range.

Domain Classifier Reliability

All estimators except Unweighted DM use density-ratio weights computed from the domain classifier’s predicted probabilities (Section 3.4), so their results depend on the quality of the classifier. We test this dependence by removing the classifier’s calibration step and by masking the ad features it sees, and measure the effect on the downstream metrics of Experiment 1: Top-1 accuracy, Top-1 regret, and Value MAE%. Each classifier variant below is evaluated on the same 350 trials of Experiment 1, with everything else fixed:

• Experiment 1 DC: the classifier of Experiment 1 (Appendix § 8.4), trained on its own fold, disjoint from the reward model’s (cross-fitting), and temperature-calibrated on 5-fold out-of-fold logits.

• Uncalibrated DC: Experiment 1 DC without temperature calibration.

• Feature Masked DC: Experiment 1 DC with one, two, or all three ad features set to zero (33%, 67%, and 100% ad masked). With all three masked, only the user features remain, and these are the same under every policy, so the classifier cannot tell the policies apart.

Table 7 shows the results. Unweighted DM does not use the classifier, so its results are omitted here. Experiment 1 DC and Uncalibrated DC perform about the same for every estimator, so calibration has little effect on the downstream metrics. Masking the ad features degrades them: as 33%, 67%, and 100% of the ad features are masked, the Top-1 accuracy of Weighted DM falls from 0.90 to 0.86, 0.83, and 0.84, that of Weighted DR from 0.94 to 0.86, 0.81, and 0.84, and that of IPS from 0.62 to 0.27. Per-policy Weighted DM has lower Top-1 accuracy than Weighted DM for every variant except full masking, where both reach 0.84. With all ad features masked, the weighted estimators end close to their unweighted counterparts.

Table 8 reports five measures of the classifier itself, to test whether they reveal this degradation without the downstream metrics. NLL is the negative log-likelihood of the classifier’s predicted probability for the true policy on held-out impressions. Cand. acc. is the fraction of held-out candidate impressions for which the classifier ranks the candidate that produced them first among the candidates. Ratio corr. is the rank correlation between the estimated and the true density ratios, averaged over candidates. Est. ESS is $\mathrm{ESS}/n$ of the estimated mixture weights (Equation (11)). Cold-start err. is the absolute difference between the estimated and the true cold-start mass at $\tau= 0.1$. Ratio correlation and cold-start error need the true policies, so they are available only in simulation. Removing calibration leaves all five measures essentially unchanged, consistent with its small downstream effect. Masking the ad features moves them with the downstream degradation:

Table 7: Estimator performance under five domain-classifier variants over 50 seeds. Each estimator cell reports Top-1 accuracy / Top-1 regret / Value MAE% (Acc / Reg / MAE%). Lower Reg and MAE% are better; higher Acc is better. Best displayed value for each metric within each estimator column is in bold; ties are all bolded.

DC variant	IPS Acc ↑ / Reg ↓ / MAE% ↓	Weighted DM Acc ↑ / Reg ↓ / MAE% ↓	Per-policy Weighted DM Acc ↑ / Reg ↓ / MAE% ↓	Unweighted DR Acc ↑ / Reg ↓ / MAE% ↓	Weighted DR Acc ↑ / Reg ↓ / MAE% ↓
Experiment 1 DC	0.62 / 0.0052 / 5.56	0.90 / 0.0005 / 2.16	0.82 / 0.0016 / 2.92	0.90 / 0.0008 / 1.17	0.94 / 0.0002 / 0.73
Uncalibrated DC	0.59 / 0.0051 / 5.46	0.90 / 0.0006 / 2.47	0.84 / 0.0012 / 2.97	0.89 / 0.0007 / 1.14	0.93 / 0.0003 / 0.71
Feature Masked DC (33%)	0.55 / 0.0106 / 7.85	0.86 / 0.0014 / 2.52	0.83 / 0.0014 / 2.61	0.86 / 0.0013 / 2.30	0.86 / 0.0012 / 2.41
Feature Masked DC (67%)	0.33 / 0.0271 / 9.53	0.83 / 0.0019 / 3.09	0.80 / 0.0022 / 2.99	0.82 / 0.0017 / 3.48	0.81 / 0.0020 / 3.83
Feature Masked DC (100%)	0.27 / 0.0315 / 10.45	0.84 / 0.0018 / 3.43	0.84 / 0.0015 / 3.50	0.83 / 0.0019 / 4.79	0.84 / 0.0018 / 4.56

tbl:8: Domain-classifier reliability diagnostics for the five classifier variants. Oracle ratio correlation and cold-start error are available only in simulation; the ratio correlation is undefined under full masking, where the estimated weights are constant. Lower NLL and cold-start error are better; higher candidate accuracy and ratio correlation are better. Best displayed value for each directional metric is in bold; ties are all bolded.

DC variant	NLL ↓	Cand. acc. ↑	Ratio corr. ↑	Est. ESS	Cold-start err. ↓
Experiment 1 DC	1.71	0.32	0.47	0.59	0.16
Uncalibrated DC	1.71	0.32	0.47	0.58	0.16
Feature Masked DC (33%)	1.77	0.29	0.37	0.69	0.21
Feature Masked DC (67%)	1.84	0.24	0.24	0.81	0.27
Feature Masked DC (100%)	1.91	0.18	–	1.00	0.39

NLL rises from 1.71 to 1.91, candidate accuracy falls from 0.32 to 0.18, ratio correlation falls from 0.47 to 0.24 at 67% masking (it is undefined at 100%, where the estimated weights are constant), and cold-start error rises from 0.16 to 0.39. The estimated ESS instead rises from 0.59 to 1.00: the weights flatten because the classifier loses the ad features, not because overlap improves. A high ESS therefore indicates good overlap only when the classifier can tell the policies apart. NLL and candidate accuracy flag when it cannot without the oracle, but cannot tell whether the policies are genuinely similar or the features are missing; in simulation, ratio correlation and cold-start error separate these cases.

Production Data: Per-Policy Breakdown

We present the per-policy results of the production experiment in Section 5. Table 9 reports the Value MAE% of each estimator for each policy, where $P_1$ is the logging policy and $P_2$–$P_6$ are the five candidates; as in Table 2, estimated weights are clipped at $c = 20$ and all values are averaged over 50 random subsamples. Among the DM estimators, Weighted DM has a lower Value MAE% than Unweighted DM on every candidate (10.91–12.24 versus 13.30–15.19) and a lower Value MAE% than Per-policy Weighted DM on four of the five candidates, the exception being $P_6$ (10.91 versus 10.51). IPS and both DR estimators have a lower Value MAE% than all DM estimators on every candidate: Unweighted DR ranges from 1.90 to 2.48 and Weighted DR from 2.02 to 2.81, while IPS is lowest on $P_2$ and $P_4$ (1.87) but reaches 6.87–7.31 on $P_3$, $P_5$, and $P_6$. On the logging policy $P_1$, the density ratio is identically one, so IPS and both DR estimators reduce to the mean of the logged rewards and have zero error by construction, and Per-policy Weighted DM coincides with Unweighted DM (14.40).

Policy	IPS	Unweighted DM	Weighted DM	Per-policy Weighted DM	Unweighted DR	Weighted DR
P$_1$ (logging)	0.00 ± 0.00	14.40 ± 1.45	11.94 ± 1.40	14.40 ± 1.45	0.00 ± 0.00	0.00 ± 0.00
P$_2$	1.87 ± 0.18	15.19 ± 1.47	12.16 ± 1.44	13.42 ± 1.73	1.90 ± 0.20	2.26 ± 0.20
P$_3$	6.87 ± 0.33	13.37 ± 1.33	11.00 ± 1.31	12.16 ± 1.27	2.44 ± 0.25	2.81 ± 0.29
P$_4$	1.87 ± 0.22	14.93 ± 1.52	12.24 ± 1.39	12.75 ± 1.59	2.09 ± 0.20	2.02 ± 0.19
P$_5$	6.94 ± 0.33	13.30 ± 1.32	11.08 ± 1.25	11.36 ± 1.25	2.48 ± 0.24	2.54 ± 0.28
P$_6$	7.31 ± 0.31	13.38 ± 1.27	10.91 ± 1.24	10.51 ± 1.30	2.47 ± 0.29	2.63 ± 0.30

NeurIPS Paper Checklist

Claims

Question: Do the main claims made in the abstract and introduction accurately reflect the paper’s contributions and scope?

Answer: [Yes]

Justification: The abstract and introduction state three contributions, all delivered in the paper: (1) a mixture-weighted reward model training method using density ratios estimated from a multiclass domain classifier, requiring no logged action propensities (§ 3.3 and § 3.4); (2) a high-probability bound on each candidate’s replay Direct Method value error, separating an overlap term, a cold-start term, and a replay concentration term, and an asymptotic offline-vs-A/B routing rule derived from it (Theorem 3.3 and Corollary 3.6, Appendix § 9); and (3) empirical evaluation on a configurable simulator (Section 4) and on production traffic from a large-scale CTR system (Section 5), where the mixture-weighted reward model outperforms its unweighted counterpart in both settings. Scope and limitations of these claims (replay assumption, dependence on domain-classifier signal, asymptotic routing rule, no evaluation under live traffic) are explicitly stated in Section 6.

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• The answer [N/A] means that the abstract and introduction do not include the claims made in the paper.

• The abstract and/or introduction should clearly state the claims made, including the contributions made in the paper and important assumptions and limitations. A [No] or [N/A] answer to this question will not be perceived well by the reviewers.

• The claims made should match theoretical and experimental results, and reflect how much the results can be expected to generalize to other settings.

• It is fine to include aspirational goals as motivation as long as it is clear that these goals are not attained by the paper.

Limitations

Question: Does the paper discuss the limitations of the work performed by the authors?

Answer: [Yes]

Justification: We provide a dedicated Limitations paragraph at the end of Section 6 (Conclusions). It states the replay assumption and the assumption that an impression’s reward distribution does not depend on the policy that produced it, notes that computing the cold-start mass with the learned classifier requires calibration or error correction and that the weights help only when the representation retains policy-induced differences (Appendix § 14), and states that the routing rule is asymptotic and that its performance under live traffic is left to future work.

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• The answer [N/A] means that the paper has no limitation while the answer [No] means that the paper has limitations, but those are not discussed in the paper.

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• The authors should reflect on the scope of the claims made, e.g., if the approach was only tested on a few datasets or with a few runs. In general, empirical results often depend on implicit assumptions, which should be articulated.

• The authors should reflect on the factors that influence the performance of the approach. For example, a facial recognition algorithm may perform poorly when image resolution is low or images are taken in low lighting. Or a speech-to-text system might not be used reliably to provide closed captions for online lectures because it fails to handle technical jargon.

• The authors should discuss the computational efficiency of the proposed algorithms and how they scale with dataset size.

• If applicable, the authors should discuss possible limitations of their approach to address problems of privacy and fairness.

• While the authors might fear that complete honesty about limitations might be used by reviewers as grounds for rejection, a worse outcome might be that reviewers discover limitations that aren’t acknowledged in the paper. The authors should use their best judgment and recognize that individual actions in favor of transparency play an important role in developing norms that preserve the integrity of the community. Reviewers will be specifically instructed to not penalize honesty concerning limitations.

Theory assumptions and proofs

Question: For each theoretical result, does the paper provide the full set of assumptions and a complete (and correct) proof?

Answer: [Yes]

Justification: All theoretical results are numbered, cross-referenced, and stated together with their assumptions. The paper contains: Definition 3.1 of the overlap and cold-start regions; Assumption 3.2, conditions A1–A4 used by Theorem 3.3; Theorem 3.3, the high-probability replay Direct Method value-error bound, with the full proof in Appendix § 9; Corollary 3.5, the top-1 selection regret bound, with proof in Appendix § 10; and Corollary 3.6, the asymptotic offline-vs-A/B routing rule, with proof in Appendix § 11.

Guidelines:

• The answer [N/A] means that the paper does not include theoretical results.

• All the theorems, formulas, and proofs in the paper should be numbered and cross-referenced.

• All assumptions should be clearly stated or referenced in the statement of any theorems.

• The proofs can either appear in the main paper or the supplemental material, but if they appear in the supplemental material, the authors are encouraged to provide a short proof sketch to provide intuition.

• Inversely, any informal proof provided in the core of the paper should be complemented by formal proofs provided in appendix or supplemental material.

• Theorems and Lemmas that the proof relies upon should be properly referenced.

Experimental result reproducibility

Question: Does the paper fully disclose all the information needed to reproduce the main experimental results of the paper to the extent that it affects the main claims and/or conclusions of the paper (regardless of whether the code and data are provided or not)?

Answer: [Yes]

Justification: For the synthetic experiments, the simulator design (user/ad feature distributions, oracle reward function, logging-policy and candidate-policy kernel parameterization), the per-trial pipeline, the value-multiplier and ESS-target grids, and the clip-threshold sweep are documented in detail in Appendix § 8, and the released code reproduces the synthetic results in Table 1 and Appendices E, F, and G (see the open-access answer below). For the production experiment, production data, embeddings, and trained production models will not be released; Section 5 documents the evaluation protocol (one logging and five candidate policies, the empirical click-through rate as each policy’s true value, 50 random data subsamples, clip $c = 20$), and the results are reported in main paper Table 2 with the per-policy breakdown in Appendix § 15.

Guidelines:

• The answer [N/A] means that the paper does not include experiments.

• If the paper includes experiments, a [No] answer to this question will not be perceived well by the reviewers: Making the paper reproducible is important, regardless of whether the code and data are provided or not.

• If the contribution is a dataset and/or model, the authors should describe the steps taken to make their results reproducible or verifiable.

• Depending on the contribution, reproducibility can be accomplished in various ways. For example, if the contribution is a novel architecture, describing the architecture fully might suffice, or if the contribution is a specific model and empirical evaluation, it may be necessary to either make it possible for others to replicate the model with the same dataset, or provide access to the model. In general, releasing code and data is often one good way to accomplish this, but reproducibility can also be provided via detailed instructions for how to replicate the results, access to a hosted model (e.g., in the case of a large language model), releasing of a model checkpoint, or other means that are appropriate to the research performed.

• While NeurIPS does not require releasing code, the conference does require all submissions to provide some reasonable avenue for reproducibility, which may depend on the nature of the contribution. For example (a) If the contribution is primarily a new algorithm, the paper should make it clear how to reproduce that algorithm. (b) If the contribution is primarily a new model architecture, the paper should describe the architecture clearly and fully. (c) If the contribution is a new model (e.g., a large language model), then there should either be a way to access this model for reproducing the results or a way to reproduce the model (e.g., with an open-source dataset or instructions for how to construct the dataset). (d) We recognize that reproducibility may be tricky in some cases, in which case authors are welcome to describe the particular way they provide for reproducibility. In the case of closed-source models, it may be that access to the model is limited in some way (e.g., to registered users), but it should be possible for other researchers to have some path to reproducing or verifying the results.

Open access to data and code

Question: Does the paper provide open access to the data and code, with sufficient instructions to faithfully reproduce the main experimental results, as described in supplemental material?

Answer: [Yes]

Justification: The simulator and synthetic evaluation code are publicly released at https://github.com/facebookresearch/ad_ranking_simulation (footnote in Section 4). Its README specifies the environment and the exact commands that reproduce Table 1 and the synthetic results in Appendices § 12, § 13 and § 14. Production data, embeddings, and trained production models will not be released.

Guidelines:

• The answer [N/A] means that paper does not include experiments requiring code.

• Please see the NeurIPS code and data submission guidelines (https://neurips.cc/public/guides/CodeSubmissionPolicy) for more details.

• While we encourage the release of code and data, we understand that this might not be possible, so [No] is an acceptable answer. Papers cannot be rejected simply for not including code, unless this is central to the contribution (e.g., for a new open-source benchmark).

• The instructions should contain the exact command and environment needed to run to reproduce the results. See the NeurIPS code and data submission guidelines (https://neurips.cc/public/guides/CodeSubmissionPolicy) for more details.

• The authors should provide instructions on data access and preparation, including how to access the raw data, preprocessed data, intermediate data, and generated data, etc.

• The authors should provide scripts to reproduce all experimental results for the new proposed method and baselines. If only a subset of experiments are reproducible, they should state which ones are omitted from the script and why.

• At submission time, to preserve anonymity, the authors should release anonymized versions (if applicable).

• Providing as much information as possible in supplemental material (appended to the paper) is recommended, but including URLs to data and code is permitted.

Experimental setting/details

Question: Does the paper specify all the training and test details (e.g., data splits, hyperparameters, how they were chosen, type of optimizer) necessary to understand the results?

Answer: [Yes]

Justification: For the synthetic experiments, Section 4 and the per-trial procedure in Appendix A.4 specify the data split (70,000 logged impressions in four disjoint folds: 20,000 for domain-classifier training, 20,000 for reward-model training, 10,000 for calibration, and 20,000 for evaluation), the architectures (one-hidden-layer MLPs with 64 units for the domain classifier and the reward models), the optimizer (Adam with learning rate 0.01 for the domain classifier and $10^{-3}$ for the reward models, batch size 512), the training epochs (4 for the domain classifier, 30 for the reward models), the temperature calibration (5-fold out-of-fold logits for the domain classifier, the calibration fold for the reward models), and the weight clip ($c = 100$), with the clip sweep in Appendix F. For the production experiment, Section 5 specifies the evaluation protocol (50 random data subsamples, clip $c = 20$) and that the shared and per-policy reward models use the same data splits, architectures, optimization, calibration, and clipping settings.

Guidelines:

• The answer [N/A] means that the paper does not include experiments.

• The experimental setting should be presented in the core of the paper to a level of detail that is necessary to appreciate the results and make sense of them.

• The full details can be provided either with the code, in appendix, or as supplemental material.

Experiment statistical significance

Question: Does the paper report error bars suitably and correctly defined or other appropriate information about the statistical significance of the experiments?

Answer: [Yes]

Justification: Main paper Table 1 reports means over the 350 synthetic trials (50 seeds $\times$ 7 ESS targets), grouped by ESS regime, and Table 2 reports means over 50 random data subsamples. Standard errors of the mean ($\mathrm{SE} = \mathrm{std}/\sqrt{n}$) are reported in the appendix breakdowns: Tables 3, 4, and 5 ($n$ is the number of trials in each realized-ESS bin), Table 6 ($n$ is the number of trials containing the candidate), Figure 1, and Table 9 ($n = 50$). The SE captures the per-trial randomness (oracle, users, ads, logging policy) for the synthetic experiments and the random data subsample for the production experiment.

Guidelines:

• The answer [N/A] means that the paper does not include experiments.

• The authors should answer [Yes] if the results are accompanied by error bars, confidence intervals, or statistical significance tests, at least for the experiments that support the main claims of the paper.

• The factors of variability that the error bars are capturing should be clearly stated (for example, train/test split, initialization, random drawing of some parameter, or overall run with given experimental conditions).

• The method for calculating the error bars should be explained (closed form formula, call to a library function, bootstrap, etc.)

• The assumptions made should be given (e.g., Normally distributed errors).

• It should be clear whether the error bar is the standard deviation or the standard error of the mean.

• It is OK to report 1-sigma error bars, but one should state it. The authors should preferably report a 2-sigma error bar than state that they have a 96% CI, if the hypothesis of Normality of errors is not verified.

• For asymmetric distributions, the authors should be careful not to show in tables or figures symmetric error bars that would yield results that are out of range (e.g., negative error rates).

• If error bars are reported in tables or plots, the authors should explain in the text how they were calculated and reference the corresponding figures or tables in the text.

Experiments compute resources

Question: For each experiment, does the paper provide sufficient information on the computer resources (type of compute workers, memory, time of execution) needed to reproduce the experiments?

Answer: [Yes]

Justification: The synthetic results were produced on CPU. On a laptop CPU, one seed takes about 3.5 minutes for Table 1 and 3 minutes for Appendix F in a single process; a seed of Appendix G takes longer because it also trains the per-policy reward models in each of its five classifier variants. The 50 seeds of each experiment are independent, so they can be split across processes. The production experiment runs on internal infrastructure, and its compute is not reported. The contribution is methodological and is not bottlenecked by specialized infrastructure.

Guidelines:

• The answer [N/A] means that the paper does not include experiments.

• The paper should indicate the type of compute workers CPU or GPU, internal cluster, or cloud provider, including relevant memory and storage.

• The paper should provide the amount of compute required for each of the individual experimental runs as well as estimate the total compute.

• The paper should disclose whether the full research project required more compute than the experiments reported in the paper (e.g., preliminary or failed experiments that didn’t make it into the paper).

Code of ethics

Question: Does the research conducted in the paper conform, in every respect, with the NeurIPS Code of Ethics https://neurips.cc/public/EthicsGuidelines?

Answer: [Yes]

Justification: The research is a methodological contribution to offline policy evaluation. The synthetic experiments use a simulator; the production experiment uses aggregated impression logs from a large-scale industrial CTR ranking system, with all per-policy results in the paper represented as $P_1$–$P_6$ and reported only as aggregate metrics. We do not release datasets, and do not introduce models intended for or applicable to surveillance, discrimination, or other prohibited use cases.

Guidelines:

• The answer [N/A] means that the authors have not reviewed the NeurIPS Code of Ethics.

• If the authors answer [No], they should explain the special circumstances that require a deviation from the Code of Ethics.

• The authors should make sure to preserve anonymity (e.g., if there is a special consideration due to laws or regulations in their jurisdiction).

Broader impacts

Question: Does the paper discuss both potential positive societal impacts and negative societal impacts of the work performed?

Answer: [N/A]

Justification: The paper is foundational methodology that improves the reliability of one specific intermediate step (offline policy evaluation) in industrial ad-ranking pipelines. It does not introduce new ML capabilities, new data sources, or new deployment surfaces, and it is not tied to any particular downstream application beyond standard ad ranking. We do not foresee direct positive or negative societal impacts of the methodological contribution itself beyond the operational reliability gains within the host ad system.

Guidelines:

• The answer [N/A] means that there is no societal impact of the work performed.

• If the authors answer [N/A] or [No], they should explain why their work has no societal impact or why the paper does not address societal impact.

• Examples of negative societal impacts include potential malicious or unintended uses (e.g., disinformation, generating fake profiles, surveillance), fairness considerations (e.g., deployment of technologies that could make decisions that unfairly impact specific groups), privacy considerations, and security considerations.

• The conference expects that many papers will be foundational research and not tied to particular applications, let alone deployments. However, if there is a direct path to any negative applications, the authors should point it out. For example, it is legitimate to point out that an improvement in the quality of generative models could be used to generate Deepfakes for disinformation. On the other hand, it is not needed to point out that a generic algorithm for optimizing neural networks could enable people to train models that generate Deepfakes faster.

• The authors should consider possible harms that could arise when the technology is being used as intended and functioning correctly, harms that could arise when the technology is being used as intended but gives incorrect results, and harms following from (intentional or unintentional) misuse of the technology.

• If there are negative societal impacts, the authors could also discuss possible mitigation strategies (e.g., gated release of models, providing defenses in addition to attacks, mechanisms for monitoring misuse, mechanisms to monitor how a system learns from feedback over time, improving the efficiency and accessibility of ML).

Safeguards

Question: Does the paper describe safeguards that have been put in place for responsible release of data or models that have a high risk for misuse (e.g., pre-trained language models, image generators, or scraped datasets)?

Answer: [N/A]

Justification: The paper releases no data and no models, and the methodological contribution (offline policy evaluation via mixture-weighted reward modeling) does not produce assets with a high risk of misuse such as pre-trained generative models, image generators, or scraped datasets.

Guidelines:

• The answer [N/A] means that the paper poses no such risks.

• Released models that have a high risk for misuse or dual-use should be released with necessary safeguards to allow for controlled use of the model, for example by requiring that users adhere to usage guidelines or restrictions to access the model or implementing safety filters.

• Datasets that have been scraped from the Internet could pose safety risks. The authors should describe how they avoided releasing unsafe images.

• We recognize that providing effective safeguards is challenging, and many papers do not require this, but we encourage authors to take this into account and make a best faith effort.

Licenses for existing assets

Question: Are the creators or original owners of assets (e.g., code, data, models), used in the paper, properly credited and are the license and terms of use explicitly mentioned and properly respected?

Answer: [N/A]

Justification: The paper does not use externally-licensed datasets or models. The synthetic experiments use a custom-built simulator developed by the authors, and the production experiment uses internal proprietary impression logs from the host institution’s CTR ranking system; no third-party assets requiring license attribution are used.

Guidelines:

• The answer [N/A] means that the paper does not use existing assets.

• The authors should cite the original paper that produced the code package or dataset.

• The authors should state which version of the asset is used and, if possible, include a URL.

• The name of the license (e.g., CC-BY 4.0) should be included for each asset.

• For scraped data from a particular source (e.g., website), the copyright and terms of service of that source should be provided.

• If assets are released, the license, copyright information, and terms of use in the package should be provided. For popular datasets, paperswithcode.com/datasets has curated licenses for some datasets. Their licensing guide can help determine the license of a dataset.

• For existing datasets that are re-packaged, both the original license and the license of the derived asset (if it has changed) should be provided.

• If this information is not available online, the authors are encouraged to reach out to the asset’s creators.

New assets

Question: Are new assets introduced in the paper well documented and is the documentation provided alongside the assets?

Answer: [Yes]

Justification: The paper releases the simulator and synthetic evaluation code at https://github.com/facebookresearch/ad_ranking_simulation. Its README documents the environment, the commands that reproduce each synthetic table and figure, and the code layout, and the code is released under the CC BY-NC 4.0 license included in the repository.

Guidelines:

• The answer [N/A] means that the paper does not release new assets.

• Researchers should communicate the details of the dataset/code/model as part of their submissions via structured templates. This includes details about training, license, limitations, etc.

• The paper should discuss whether and how consent was obtained from people whose asset is used.

• At submission time, remember to anonymize your assets (if applicable). You can either create an anonymized URL or include an anonymized zip file.

Crowdsourcing and research with human subjects

Question: For crowdsourcing experiments and research with human subjects, does the paper include the full text of instructions given to participants and screenshots, if applicable, as well as details about compensation (if any)?

Answer: [N/A]

Justification: The paper does not involve crowdsourcing or research with human subjects. The synthetic experiments use a simulator with no real users; the production experiment analyzes pre-existing aggregated impression logs from a deployed industrial CTR ranking system without any new human-subject data collection.

Guidelines:

• The answer [N/A] means that the paper does not involve crowdsourcing nor research with human subjects.

• Including this information in the supplemental material is fine, but if the main contribution of the paper involves human subjects, then as much detail as possible should be included in the main paper.

• According to the NeurIPS Code of Ethics, workers involved in data collection, curation, or other labor should be paid at least the minimum wage in the country of the data collector.

Institutional review board (IRB) approvals or equivalent for research with human subjects

Question: Does the paper describe potential risks incurred by study participants, whether such risks were disclosed to the subjects, and whether Institutional Review Board (IRB) approvals (or an equivalent approval/review based on the requirements of your country or institution) were obtained? Answer: [N/A]

Justification: The paper does not involve research with human subjects; no IRB or equivalent approval was required.

Guidelines:

• The answer [N/A] means that the paper does not involve crowdsourcing nor research with human subjects.

• Depending on the country in which research is conducted, IRB approval (or equivalent) may be required for any human subjects research. If you obtained IRB approval, you should clearly state this in the paper.

• We recognize that the procedures for this may vary significantly between institutions and locations, and we expect authors to adhere to the NeurIPS Code of Ethics and the guidelines for their institution.

• For initial submissions, do not include any information that would break anonymity (if applicable), such as the institution conducting the review.

Declaration of LLM usage

Question: Does the paper describe the usage of LLMs if it is an important, original, or non-standard component of the core methods in this research? Note that if the LLM is used only for writing, editing, or formatting purposes and does not impact the core methodology, scientific rigor, or originality of the research, declaration is not required.

Answer: [N/A]

Justification: The core method development in this research does not involve large language models as any important, original, or non-standard component. The proposed estimators (mixture-weighted reward modeling, density-ratio estimation via a multiclass domain classifier, doubly-robust estimation) are statistical and do not use LLMs.

Guidelines:

• The answer [N/A] means that the core method development in this research does not involve LLMs as any important, original, or non-standard components.

• Please refer to our LLM policy in the NeurIPS handbook for what should or should not be described.