{"id":"f44ad29a-bd75-4564-b002-5eaf8456281c","arxiv_id":"2505.23954","paper_version":1,"verdict":"CONDITIONAL","confidence":"MODERATE","novelty_score":6.0,"correctness_risk":"medium","formal_verification":"none","parameter_count":3,"one_line_summary":"A causal estimator identifies the misreporting rate as the ratio of the gap between nominal and true feature effects to the true causal effect of the feature on an outcome.","lead":"This paper derives a formula for estimating how often agents misreport their features, by comparing causal effects computed from manipulated and unmanipulated data. A smart generalist might care because it offers a low-cost way to measure gaming such as Medicare upcoding in ML-driven resource allocation.","discovery_kind":"new_method","skeptic_critique":{"model":"deepseek-v4-flash","headline":"Theorem 1 depends on Assumption 4, which is untestable and likely violated in the Medicare application because genuine modification can change the conditional effect of a diagnosis on mortality; the paper's negative control does not isolate this assumption.","rationale":"The reader's weakest_assumption identifies Assumption 4, and my reading agrees that this is the most fragile load-bearing condition in Theorem 1. The proof uses Assumption 4 twice: once to set τ′_a = τ*_a and once, together with the conditional-independence structure, to set δ′_a = δ*_a. If Assumption 4 fails, the estimator becomes (τ*_a + bias_1 - τ_a)/(δ*_a + bias_2), so the reported MR is biased in an unknown direction. This is not merely an abstract identifiability caveat: in the flagship Medicare application, the manipulated population (switchers to private insurers) and the unmanipulated population (Traditional Medicare stayers) are selected differently, and the insurers' genuine modifications can alter the effect of a diagnosis on mortality. The paper's Limitations section flags unobserved confounding but not Assumption 4, which makes the gap easy to overlook. I considered whether an even more basic concern, the absence of a causal path from X to Y in the DAGs, is more load-bearing, since reported features can influence payments and hence mortality. That concern is real, but the paper explicitly defines the downstream variable to be a causal descendant of X* only; testing it would require a different research design. Assumption 4 is the weakest link in the stated theorem and is directly checkable on the nonpayment HCCs, so I recommend that the verdict remain CONDITIONAL on a direct test of Assumption 4. The proposed concrete test is feasible with the data already used in the paper and would either support or undermine the invariance assumption in a way the current negative-control validation cannot.","tokens_in":27115,"tokens_out":20636,"duration_ms":264039,"concrete_test":"Using the same CMS claims data, restrict to nonpayment HCCs for which X = X* in D because there is no incentive to misreport. Fit CATE estimators θ*(c) on TM-stayer data D* and θ_a(c) on switcher data D, using identical covariates C (demographics plus prior-year HCCs), identical model classes, and identical sample-splitting. Compare the two estimated CATE surfaces on the common support of C using a standardized discrepancy measure, e.g., a weighted mean squared difference across strata of C or a permutation test of the stratified difference. Repeat the comparison within subgroups defined by prior-year HCC burden, where genuine modification is most likely to change mortality effects.","verdict_should_be":"UNCHANGED","load_bearing_attack":"Assumption 4 is the load-bearing bridge in Theorem 1: it is the only step that replaces the unidentifiable τ*_a and δ*_a with the identifiable τ′_a and δ′_a. It requires E_Pa[Y(1)-Y(0)|C=c] = E_P*[Y(1)-Y(0)|C=c] for every c. In the Medicare application, D* is Traditional Medicare stayers and D is switchers to private insurers; these populations differ in health trajectories and care. Genuine modification, the very phenomenon the method is designed to accommodate, can directly change the CATE: if an insurer's care program reduces mortality among enrollees with a given HCC, the conditional effect of that HCC on death is smaller in Pa than in P* even after conditioning on demographics and prior-year HCCs. Selection into switching can cause the same violation. The reported nonpayment-HCC negative control only tests the full estimator, not Assumption 4 by itself, and payment HCCs are precisely the codes most likely to be targeted by genuine modification. Thus the headline MR estimates for payment HCCs (e.g., HCC21: 0.165, CI [0.054, 0.241]) are credible only if Assumption 4 happens to hold, and the paper provides no direct evidence that it does.","agreement_with_reader":"agree"},"referee_report":{"model":"deepseek-v4-flash","summary":"The paper proposes a causal estimator for the rate at which strategic agents misreport a binary feature X* (the misreporting rate, MR = P_a(X*=0|X=1)) when the true feature is unobserved, in settings where agents may also genuinely modify the feature. The key idea is that genuine modification changes the causal descendants of X*, whereas misreporting of X does not affect the downstream outcome Y. Under Assumptions 1-4, the paper proves in Theorem 1 that MR = (τ'_a - τ_a)/δ'_a, where τ_a is the nominal effect of reported X on Y in the manipulated data, τ'_a is the true effect of X* on Y transported from unmanipulated data, and δ'_a is the true effect for the X*=0 group. The paper also provides an asymptotic variance formula (Theorem 2) and validates the method on a semi-synthetic loan-fraud simulation and on Medicare claims data, where the estimator is used to compare misreporting of payment versus nonpayment HCCs.","tokens_in":27382,"tokens_out":9229,"duration_ms":85613,"significance":"If the identification result holds, the paper offers a useful new tool for auditing and strategic classification: it estimates an aggregate misreporting rate without observing true features and without per-agent audits, using only a manipulated dataset and an unmanipulated dataset. The causal framing is elegant, and the paper gives a formal identifiability proof, a variance characterization that guides feature choice, and extensive semi-synthetic experiments with several baselines. The proof of Theorem 1 is algebraically sound under the stated assumptions, and the paper is honest about the need for no unobserved confounding. However, the practical value depends critically on Assumption 4 (transportability of conditional average treatment effects from the unmanipulated to the manipulated population), which is not validated in the real-data demonstration; the Medicare analysis also lacks ground truth and uses post-hoc selection on the very quantities entering the estimator. These issues do not invalidate the theoretical core but do limit the strength of the empirical claims.","major_comments":[{"comment":"Assumption 4 is the only bridge that replaces the unidentifiable τ*_a and δ*_a with the identifiable τ'_a and δ'_a in the proof of Theorem 1 (Appendix B.2). In the Medicare application, D* is Traditional Medicare stayers and D is switchers to private insurers; these populations differ in care and health trajectories, and the genuine modification that the method is designed to accommodate can itself change the conditional effect of an HCC on mortality. The nonpayment-HCC negative control in §5.2/Figure 3 tests the full estimator on HCCs with no payment incentive; it does not validate Assumption 4 for the payment HCCs, which are precisely the ones for which modification incentives exist. Please add a sensitivity analysis (e.g., bounds on MR as a function of the degree of violation of Assumption 4) or direct evidence that the relevant CATEs transport from TM stayers to MA switchers, and state plainly that the Medicare point estimates are conditional on untestable transportability.","section":"Section 3 (Assumption 4); Section 4.1 (Theorem 1); Section 5.2"},{"comment":"The proofs use an unstated random-misreporting assumption: in Step 2 of Lemma 1 (Appendix B.1) and in the proof of Theorem 1 (Appendix B.2), P_a(C|X*=0,X=1) is replaced by P_a(C|X*=0), which requires C⊥X|X*,A. The text states this informally ('the misreported group will be a random sample of the group where X*=0') but it is not listed among Assumptions 1-4 and is not defended in the Medicare application, where upcoding decisions may depend on enrollee demographics and prior HCCs. If misreporting is targeted based on C, the equality fails and the estimator is biased; please state this assumption explicitly and discuss its plausibility, or relax it.","section":"Section 4.1 (Lemma 1); Appendix B.1-B.2"},{"comment":"The real-data demonstration has no ground truth, and the HCC selection rule is applied after estimating the same quantities that enter the estimator: only HCCs with at least 1% prevalence and an estimated causal effect δ' > 0.1 are reported (Section 5.2 and Tables 1-2). This post-hoc selection is not accounted for in the bootstrap confidence intervals, so the 'sanity check' for nonpayment HCCs is not a falsifiable validation of the method. Please report the full set of HCCs (or pre-specify the selection rule) and explicitly frame the Medicare results as assumption-dependent estimates rather than measured misreporting rates.","section":"Section 5.2; Tables 1-2"}],"minor_comments":[{"comment":"The statement 'P_a(X=1|X*=0) = (τ'_a - τ_a)/δ'_a × P_a(X=1)' is algebraically inconsistent with the proof, which derives a ratio involving P_a(X=0) + P_a(X=1,X*=0); please correct the stated formula.","section":"Appendix C, Corollary A2"},{"comment":"There are several typos ('Defnition', 'rearanging', 'maximume', 'eduction'); please proofread the manuscript carefully.","section":"Throughout"},{"comment":"Theorem 2 assumes N=M=n, but the Medicare experiment uses very different sample sizes for D and D* (868,255 stayers versus 166,539 switchers); please clarify whether the variance formula is intended for unequal sample sizes or note that it is a simplification.","section":"Theorem 2"},{"comment":"The description of the OC-SVM baseline is inconsistent: Section 5.1 says it is trained on D* where X*=1, while Appendix E.4 says it is trained on (Y,C) from D*_1; please make the descriptions consistent.","section":"Section 5.1 and Appendix E.4"},{"comment":"The caption refers to a vertical dashed line separating nonpayment and payment HCCs, but the left panel only shows the four HCC labels; please make the figure and legend self-contained.","section":"Figure 3 caption"}],"recommendation":"major_revision","confidential_remarks":"The theoretical result is sound under the stated assumptions, and the paper could be a useful contribution after revision. The main issue is that Assumption 4 is both essential and unvalidated in the empirical application, and the real-data analysis does not provide ground truth. I would recommend asking for a sensitivity analysis around Assumption 4 and a fuller reporting of HCC selection; if those are provided convincingly, the paper could be acceptable."},"author_rebuttal":null,"desk_editor":{"model":"deepseek-v4-flash","letter":"Read 2505.23954. The core idea is genuinely new: misreporting changes the reported feature but not the causal effect of the true feature on downstream outcomes, while genuine modification does. The ratio estimator in Theorem 1 is a clean first-principles derivation and the algebra checks out. The paper also includes a real Medicare demonstration with a negative control (nonpayment HCCs), which is a meaningful empirical gesture even without ground truth.\n\nThe semi-synthetic experiments are carefully done and cover the relevant variations: amount of genuine modification, strength of the causal effect, and misreporting rate. The variance theorem is a standard delta-method result but gives useful practical guidance (use the descendant with the largest effect). The distinction from Chang et al. is correctly stated: they partially identify misreporting propensity, while this paper identifies the rate.\n\nThe soft spot is Assumption 4. The identification rests on CATE invariance between the manipulated and unmanipulated populations. In the Medicare application that is a leap: switchers are not a random sample, and genuine modification—the very thing the method is designed to accommodate—can plausibly change the conditional effect of an HCC on mortality. The negative control does not isolate Assumption 4; it only checks the full estimator on codes nobody has an incentive to fake. A reviewer should ask for sensitivity analysis or bounds under violations of Assumption 4. Also, no code or data have been released yet (the paper says code will be available), and the Medicare analysis filters HCCs post-hoc based on the same delta estimates that enter the estimator, which is a minor selection concern. These issues don't undermine the theoretical result, but they do limit how much the real-data application can support the headline claim.\n\nWho should read it: people working on strategic classification, causal auditing, or Medicare upcoding. It deserves a serious referee. The theory is sound, the simulations support the method, and the application is policy-relevant. The main revision should be an honest treatment of Assumption 4's burden, ideally with a sensitivity analysis or a partial-identification bound. Send it to review.","headline":"Clean identification argument and a smart negative control, but Assumption 4 carries more weight than the paper acknowledges and the real-data evidence is indirect.","tokens_in":27907,"tokens_out":2889,"would_cite":true,"duration_ms":27045,"reading_group":"yes","serious_thinker":"yes","would_accept_peer_review":true},"rs_alignment":null,"lean_confirmation":null,"pith_extraction":{"msc":[],"pacs":[],"model":"deepseek-v4-flash","headline":"This paper proves the misreporting rate is identifiable from the gap between nominal and true causal effects of a feature on its downstream outcome, with no access to the true feature.","keywords":["misreporting rate","causal effect identification","strategic classification","Medicare Advantage","upcoding","risk adjustment"],"falsifier":"Audit a random sample of agents to obtain the true feature X* and the actual misreporting rate, then compare the CMRE estimate; the method is refuted if the discrepancy grows in settings where the conditional treatment effect of X* on Y is deliberately made different between the manipulated and unmanipulated populations. A simpler check: compute the MR for the same agent using two different downstream outcomes with large δ'_a; if the two estimates disagree beyond sampling error, the identifying assumptions fail.","tokens_in":26941,"feed_emoji":"🔎","tokens_out":8656,"duration_ms":74094,"temperature":0.7,"pith_summary":"The paper claims that the average rate at which agents lie about a binary feature can be estimated exactly, even when agents also genuinely change that feature. The central formula equates the misreporting rate P_a(X* = 0 | X = 1) with the ratio (τ'_a − τ_a)/δ'_a, where τ_a is the apparent causal effect of the reported feature on a downstream outcome, τ'_a is the true causal effect of the underlying feature transported from a clean dataset, and δ'_a is the true effect among the group without the genuine feature. The identification works because genuine modification changes downstream outcomes while misreporting does not. If correct, the result turns 'upcoding' and similar gaming behaviors into quantities measurable from two datasets, without ever observing the true feature.","feed_headline":"Misreporting rate equals a ratio of causal effects","feed_subtitle":"Lies change reported features but not their effects; the gap reveals how often agents game the system.","key_machinery":"The load-bearing object is the ratio identity MR_a = (τ'_a − τ_a)/δ'_a, operationalized as the Causal Misreporting Estimator (CMRE). The three ingredients are: τ_a, the nominal average causal effect of the reported feature X on the outcome Y among the reported group (computed from manipulated data); τ'_a, the true average causal effect of the unobserved feature X* on Y, learned from unmanipulated data and averaged over the same reported group's confounder distribution; and δ'_a, that same true effect averaged over the X* = 0 group that could be misreported. The mechanism is the descendant asymmetry: genuine modification alters Y through X*, while misreporting alters only X, leaving Y untouched — so the gap between nominal and true effects is exactly the misreporting rate times the effect on the misreported group.","core_discovery":"Under Assumptions 1–4, the paper proves Theorem 1: for δ'_a ≠ 0, the misreporting rate P_a(X* = 0 | X = 1) is identifiable from two datasets and equals (τ'_a − τ_a)/δ'_a. The proof shows that the nominal effect τ_a of the reported X on the descendant Y decomposes into the true effect τ'_a minus the misreporting rate times the true effect δ'_a on the misreported group; this decomposition relies on the fact that misreported features have no causal effect on descendants, so any discrepancy between nominal and true effects is attributable solely to lying. Assumption 4, which posits that conditional treatment effects of X* on Y are identical across the manipulated and unmanipulated populations, allows replacing the unobservable τ*_a and δ*_a with τ'_a and δ'_a estimated from clean data. The paper further derives the asymptotic variance of the estimator (Theorem 2), showing that the variance grows without bound as δ'_a approaches zero.","pith_inferences":["A natural next use is triage: run CMRE on all agents to produce a misreporting rate per feature, then target expensive manual audits only at agents whose estimated rate is high, using the estimate as a cheap prior for where to look.","The same ratio identity could be combined with sensitivity analysis for unobserved confounding; the authors flag no-unmeasured-confounding as a limitation, but existing bounds on treatment effects could turn the point estimate into an interval.","A falsifiable consistency check within a single application would compute the MR using two different downstream outcomes Y1 and Y2; if the causal assumptions hold and both effects are nonzero, the point estimates should agree, giving a data-driven diagnostic for Assumption 4.","The insight may generalize beyond binary features to multivalued or continuous reports by aggregating over thresholds, though the paper only treats binary X."],"forward_implications":["A decision maker can estimate each agent's average misreporting rate per feature using only the manipulated dataset plus an unmanipulated dataset (e.g., pre-deployment or government data), with no access to true features or audit labels.","Among available downstream variables, the one with the largest causal effect δ'_a on the outcome should be used; the variance analysis shows estimates become unstable as δ'_a approaches zero.","The identifiability of P_a(X* = 0 | X = 1) extends directly to other estimands: the false positive rate P_a(X = 1 | X* = 0) and the marginal difference P_a(X = 1) − P_a(X* = 1) are also identifiable.","Empirically, the method reproduces the expected pattern in Medicare Advantage: non-payment HCCs (no incentive to lie) have misreporting rates indistinguishable from zero, while payment HCCs show significantly positive rates, whereas baseline methods give implausible estimates.","The method applies without change to settings with selection bias, unobserved confounding between agent and outcome, or mediator-based genuine modification, per the DAGs in Appendix A."],"supporting_citations":[{"why":"Closest prior work; ranks agents by misreporting propensity but only partially identifies the rate, and conflates misreporting with genuine modification.","marker":"[5]"},{"why":"Establishes the causal-modeling view of strategic classification and the improvement/gaming distinction that the paper builds on.","marker":"[31]"},{"why":"Supplies the Neyman-Rubin potential outcomes notation and assumptions used in defining τ_a, τ'_a, δ'_a and in the proof.","marker":"[37]"},{"why":"Provides the S-learner metalearner used to estimate conditional average treatment effects θ*(c) and θ_a(c) in the CMRE estimator.","marker":"[26]"},{"why":"Empirical evidence of upcoding in Medicare Advantage that motivates the problem and grounds the real-data interpretation.","marker":"[13]"},{"why":"Defines the CMS-HCC risk adjustment model that determines which features (payment HCCs) agents would have incentive to misreport.","marker":"[36]"}],"fun_headline_variants":["Lies leave no causal trace—the gap reveals lie rate","Causal comparison exposes agent misreporting rate","Misreporting rate emerges from causal effect gap","Deceptive features have no effect—count the lies","Genuine vs deceptive: causal test quantifies lying"],"cache_read_input_tokens":3200,"weakest_assumption_plain":"The load-bearing premise is that the conditional effect of the true feature on the outcome is identical in the potentially-misreporting population and the clean comparison population; if genuine modification by agents changes how the true feature affects the outcome, the estimate is biased.","fun_headline_variants_meta":{"raw":{"variants":["Lies leave no causal trace—the gap reveals lie rate","Causal comparison exposes agent misreporting rate","Misreporting rate emerges from causal effect gap","Deceptive features have no effect—count the lies","Genuine vs deceptive: causal test quantifies lying"]},"model":"deepseek-v4-flash","effort":"low","cost_usd":0.001343,"raw_usage":{"total_tokens":5457,"prompt_tokens":946,"completion_tokens":4511,"prompt_tokens_details":{"cached_tokens":384},"prompt_cache_hit_tokens":384,"prompt_cache_miss_tokens":562,"completion_tokens_details":{"reasoning_tokens":4434}},"tokens_in":562,"tokens_out":4511,"duration_ms":28317,"temperature":1.0,"reasoning_tokens":4434,"cache_read_input_tokens":384,"cache_creation_input_tokens":0},"cache_creation_input_tokens":0},"created_at":"2026-08-07T12:37:54.125990+00:00","model_set":{"reader":"deepseek-v4-flash"},"falsifier":"Audit a random sample of agents to obtain the true feature X* and the actual misreporting rate, then compare the CMRE estimate; the method is refuted if the discrepancy grows in settings where the conditional treatment effect of X* on Y is deliberately made different between the manipulated and unmanipulated populations. A simpler check: compute the MR for the same agent using two different downstream outcomes with large δ'_a; if the two estimates disagree beyond sampling error, the identifying assumptions fail.","supporting_citations":[{"cited_title":"Who’s gaming the system? a causally-motivated approach for detecting strategic adaptation.Advances in Neural Information Processing Systems, 37:42311–42348, 2024","cited_arxiv_id":null,"evidence_quote":"Closest prior work; ranks agents by misreporting propensity but only partially identifies the rate, and conflates misreporting with genuine modification."},{"cited_title":"Strategic classification is causal modeling in disguise","cited_arxiv_id":null,"evidence_quote":"Establishes the causal-modeling view of strategic classification and the improvement/gaming distinction that the paper builds on."},{"cited_title":"Causal inference using potential outcomes.Journal of the American Statistical Association, 100(469):322–331, 2005","cited_arxiv_id":null,"evidence_quote":"Supplies the Neyman-Rubin potential outcomes notation and assumptions used in defining τ_a, τ'_a, δ'_a and in the proof."},{"cited_title":"Upcoding: evidence from medicare on squishy risk adjustment.Journal of Political Economy, 128(3):984–1026, 2020","cited_arxiv_id":null,"evidence_quote":"Empirical evidence of upcoding in Medicare Advantage that motivates the problem and grounds the real-data interpretation."},{"cited_title":"Risk adjustment of medicare capitation payments using the cms-hcc model.Health care financing review, 25(4):119, 2004","cited_arxiv_id":null,"evidence_quote":"Defines the CMS-HCC risk adjustment model that determines which features (payment HCCs) agents would have incentive to misreport."}],"review_version":1}