A Cautionary Tale on Integrating Studies with Disparate Outcome Measures for Causal Inference
Authors: Harsh Parikh
Trang Quynh Nguyen
Elizabeth Stuart
Kara E. Rudolph
Caleb H Miles
Venue: NeurIPS 2025 poster ()
Keywords: causal inference
data integration
semiparametric statistics
double robustness
Primary area: probabilistic_methods
TL;DR: If and when integrating studies with different outcome measures improves efficiency, showing that gains hinge on strong linking assumptions but carry bias risks, while weaker ones may offer finite-sample benefits.

Abstract: Data integration approaches are increasingly used to enhance the efficiency and generalizability of studies. However, a key limitation of these methods is the assumption that outcome measures are identical across datasets -- an assumption that often does not hold in practice. Consider the following opioid use disorder (OUD) studies: the XBOT trial and the POAT study, both evaluating the effect of medications for OUD on withdrawal symptom severity (not the primary outcome of either trial). While XBOT measures withdrawal severity using the subjective opiate withdrawal scale, POAT uses the clinical opiate withdrawal scale. We analyze this realistic yet challenging setting where outcome measures differ across studies and where neither study records both types of outcomes. Our paper studies whether and when integrating studies with disparate outcome measures leads to efficiency gains. We introduce three sets of assumptions -- with varying degrees of strength -- linking both outcome measures. Our theoretical and empirical results highlight a cautionary tale: integration can improve asymptotic efficiency only under the strongest assumption linking the outcomes. However, misspecification of this assumption leads to bias. In contrast, a milder assumption may yield finite-sample efficiency gains, yet these benefits diminish as sample size increases. We illustrate these trade-offs via a case study integrating the XBOT and POAT datasets to estimate the comparative effect of two medications for opioid use disorder on withdrawal symptoms. By systematically varying the assumptions linking the SOW and COW scales, we show potential efficiency gains and the risks of bias. Our findings emphasize the need for careful assumption selection when fusing datasets with differing outcome measures, offering guidance for researchers navigating this common challenge in modern data integration.

A Cautionary Tale on Integrating Studies with Disparate Outcome Measures for Causal Inference
Harsh Parikh Yale University harsh. prrrsh.aarihhyaee.com edu
Trang Quynh Nguyen Johns Hopkins University trang nguyen@jhu. edu
Elizabeth Stuart Johns Hopkins University estuart@jhu edu
Kara Rudolph Columbia University
Caleb Miles
Columbia University cm38250cumc. columbia. edu
kr28548cumc. columbia.edi edu
Abstract
Data integration approaches are increasingly used enhance the efficiency and generalizability of studies. However, a key limitation of these methods is the assumption that outcome measures identical across datasets assumption that often does not hold in practice. Consider the following opioid use disorder (OUD) studies: the XBOT trial and the POAT study, both evaluating the effect of medications for OUD on withdrawal symptom severity (not the primary outcome either trial). While XBOT measures withdrawal severity using the subjective opiate withdrawal scale, POAT uses the clinical opiate withdrawal scale. We analyze this realistic yet challenging setting where outcome measures differ across studies and where neither study records both types of outcomes. Our paper studies whether and when integrating studies with disparate outcome measures leads to efficiency gains. We introduce three sets of assumptions with varying degrees of strength linking both outcome measures. Our theoretical and empirical results highlight cautionary tale: integration under the strongest assumption linking the outcomes. However, misspecification of this assumption leads to bias. In contrast, milder assumption may yield finite- sample efficiency gains, yet these benefits diminish as sample size increases. We illustrate these trade-offs via to estimate the comparative effect of two medications for opioid use disorder on withdrawal symptoms. By systematically varying the assumptions linking the SOW and COW scales, we show potential efficiency gains and the risks of bias. Our findings emphasize the need for careful assumption selection when fusing datasets with differing outcome measures, offering guidance for researchers navigating this common challenge in modern data integration.
improve asymptotic efficiency only
study integrating the XBOT and POAT datasets
1 Introduction
Robust decision-making increasingly depends on integrating information from diverse sources practice commonly referred to as data integration. By harnessing complementary datasets, researchers can improve the accuracy, generalizability, and efficiency of statistical inference (Bareinboim and Pearl, 2016). In the realm of causal inference, data integration has emerged as a central focus, recently cited among the top ten priorities for advancing the field (Mitra al., 2022). This surge of interest reflects its wide-ranging utility: from generalizing or transporting evidence (Degtiar and Rose, 2023: Parikh et al., 2024; Huang and Parikh, 2024), to heterogeneous causal effect estimation (Brantner
39th Conference on Neural Information Processing Systems (NcurIPS 2025).

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et al., 2023), boosting statistical efficiency (Rosenman et al., 2023), and mitigating bias (Kallus et al., 2018).
However, in many real-world scenarios, various data sources may capture outcomes that, while related, are not identical to those measured in the trial. For example, in studies medications for opioid use disorder (MOUD), the intensity of withdrawal symptoms can be measured using two different scales: the Clinical Opiate Withdrawal Scale (COWS) and the Subjective Opiate Withdrawal Scale (SOWS) (Wesson and Ling, 2003; Handelsman et al., 1987). In the XBOT trial that compared the effectiveness of injection naltrexone to sublingual buprenorphine returning to regular opioid use, withdrawal symptoms were measured using SOWS (Lee et al., 2018) 8). However, the POATS study, which compared the effectiveness of adding counseling sublingual buprenorphine treatment, used COWS to measure the strength of withdrawal symptoms (Weiss et al., 2010). Despite the differences in outcome measures, researchers might wish to leverage the POATS study to improve the precision of treatment effect estimates in the XBOT trial (or vice versa). This raises an important question: when can integration of primary study and auxiliary data with disparate outcome measures yield efficiency gains for causal effect estimates if neither study has observation of both outcome measures on the same group of individuals?
terms of reducing risks of
Contributions. Our paper addresses this question by examining scenarios in which neither the trial nor the auxiliary data records both outcome measures on the same set of individuals.
We formulate principal assumption that connects the primary outcome in the trial with the auxiliary outcome in external data, offering conceptual "license" to borrow strength from auxiliary sources. We present three versions of this assumption ranging from strong weak thereby providing flexible framework that reflects varying degrees of identifiability.
We characterize the conditions under which integrating studies can improve semiparametric effi- ciency as well as finite sample gains. We show that asymptotic gains are only possible under the strongest assumptions (albeit at a risk of some bias). However, under milder (and perhaps more realistic) conditions, finite-sample improvements may be realized, although these benefits diminish as sample sizes grow.
We illustrate these insights through simulation studies and a real-world case study from the MOUD trial. Our findings underscore both the promise and the limitations of using auxiliary data with non-overlapping outcomes. Importantly, we provide practical guidance for researchers aiming to navigate these tradcoffss in applied causal inference settings.
In a nutshell, this paper presents a cautionary framework for data integration in the presence of disparate outcomes, showing that while such integration may yield marginal gains under ideal conditions, it carries significant risk of bias when assumptions are violated - as illustrated by our case study. To the best of our knowledge, we present the first formal quantification of this tradeoff, emphasizing the need for scrutiny before applying such methods in practice.
The paper is organized as follows. Section 3 introduces the notation, setup, and standard assumptions. Section presents the key structural assumption linking primary and auxiliary outcomes, along with three scenarios that reflect varying degrees of prior knowledge about this relationship. Sections 4.2- 4.4 contains our main theoretical contributions: semiparametric efficiency bounds under each scenario, as well worst-case bounds on finile-smpll estimation errors. In Section 5, we apply these methods to estimate the causal effect of medications for opioid use disorder (MOUD) on withdrawal severity, using SOWS (from the XBOT trial) and COWS (from the POAT study). Section 6 concludes with a summary of key findings, limitations, and directions for future research. Appendix presents simulation results evaluating estimator performance across varying sample sizes and dimensions. Additional theoretical discussion and proofs are provided in Appendices B, C, and D.
2 Relevant Literature
We briefly review four bodies of literature related to our work: (i) data integration causal inference, (ii) meta-analysis, (iii) data harmonization, and (iv) surrogate outcomes.
Data Integration for Causal Inference. Data integration has emerged as central focus in causal inference, recently cited among the top priorities for advancing the field (Mitra et al., 2022). It

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supports wide range of goals, including generalizing evidence across populations (Degtiar and Rose, 2023; Pearl. 2015: Parikh et al., 2024; Huang and Parikh, 2024), estimating heterogeneous effects (Brantner et al., 2023), boosting efficiency (Li and Luedtke, 2023), and mitigating bias (Kallus et al., 2018; Parikh et al., 2023b). Recent methods improve efficiency by combining auxiliary datasets while controlling bias, such as James-Stein shrinkage (Rosenman et al., 2023), semiparametric estimators (Yang et al., 2020), bias correction (Kallus et al., 2018; Yang and Ding, 2020), and Bayesian borrowing (Lin et al., 2024). However, these approaches typically assume consistent measures- - including outcomes across datasets.
Meta-Analysis and Evidence Synthesis. When outcomes differ, naïve pooling can induce substan- tial bias (Van Cleave al.. 2011). Early evidence synthesis methods, such as standardizing outcomes (Murad et al., 2019; Deeks et al., 2019), rely on strong equivalence assumptions. Traditional meta- analyses, as in (Deeks et al., 2019), uses heuristics like dichotomization or normalization, assuming commensurabillty across studies (Murad et al., 2019). More sophisticated approaches jointly model multiple outcomes, using multivariate Bayesian methods (Bujkiewicz et al., 2016) or multi-task learning analogs (Zhang and Yang, 2018). These frameworks exploit known outcome dependencies or co-measurement of outcomes to synthesize information while allowing outcome-specific variation.
Data Harmonization. Data harmonization methods are a set of tools that aim to equate measures across data sources to facilitate data integration. These methods typically align heterogencous outcomes through co-calibration (Nance et al., 2017) or latent constructs (Snavely et al., 2014). Bridge studies, where multiple outcomes are measured on the same set of individuals, can estimate mappings between outcome measures, while latent variable models treat observed outcomes noisy indicators of a shared construct. These approaches typically require both outcome measurements for the same individual and introduce additional modeling assumptions.
Leveraging Surrogate Outcomes. Another relevant literature is data integration methods leveraging studies with surrogate outcomes. For instance, Athey et al. (2019) and Ghassami et al. (2022) combine experimental data with short-term outcome measures with an observational study where long-term outcome is measured to yield a consistent estimate of the long-term treatment effect. Surrogate indices that aggregate multiple proxies can substantially improve efficiency (Ghassami et al., 2022), but rely on strong structural assumptions about the proxy moxxoo-e relationship. Existing methods generally require at least one dataset with measurement of primary and surrogate outcomes on the same set of individuals an assumption often violated in practice and one that motivates our work.
3 Preliminaries
Setup and Notations. We consider two studies: primary study (S = 0) and an auxiliary study (S = 1). The primary study observes the outcome of interest Y, while the auxiliary study observes a related but distinct outcome W. Crucially, Y and W are never observed for the same individual. In both studies, we observe treatment T {0. 1} and covariates X. Let (t) and W(t) denote the potential outcomes under treatment T = t. To unify notation, define the observed outcome as V : (1 ()Y + SW, and the observed data as O = (X, V).. We let S, {OI...., On} denote a sample of units, with and representing the number of units in the primary and auxiliary studies, respectively.
For any (random) function let (A)( denote the expectation, P. (n(((A)) = = -n f(A)) the e
empirical average, and (()(( = f f(a) (a) the population average treating ʃ as fixed. Note that [A)( integrates over randomness in both A and f, while ((f(A)) treats f as fixed. We also define the (PP) norm ||] (f))) 1/4 Futher, for compactness, we write (A = 6) = IE[A B = b] to denote the conditional expectation of A given B = b, and (B b) = E[A(t)
B b] for the conditional mean of the potential outcome A(t).
Our goal is to estimate the conditional average treatment effect (CATE): Tu(2) := n/ (X-= =x==a X) o =). and the average treulment effect (ATE): To == vy v&, both defined with respect the primary outcome Y
Assumptions & Identification We make the following assumptions:
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A.1. (S (S-ignorability) Vz, (t), - X =
A.2. (Treatment Positivity) < < P(T =t = =0) <1 for all (0.1}.
A.3. (Sampling Positivity) c << P(5= <1-c.
A.4. (Conditional Ignorability) Va,,, (()), ((t) LTI X = =
We assume the following structural models for the potential outcomes:
(()) 9 +% ? o))
(1)
(it) - (())+ 8 8~1100,0.)
where O(X) and (xX) are the treatment effect functions for Y and W. respectiivell These formulation
commonly used in the causal inference literature (Robinson, 1988: Chernozhukov et al.. 2018; Hahn et al., 2020: Rudolph et al., 2025). From Equation (I), it follows that the CATE in the primary
population is: rz( E|Y
Y (0) X ø ((x). By Assumptions A.2. and A.4., the potential outcome means v (X 2) are identified by observed data as: ( = I) = py (X =
x. T = t). Hence, the CATE is identified as: ro(2)) = juy (X x, T = 1) My X = x. = 0).
Influence Function. Let denote the collection of nuisance parameters, specifically y S), Hs (X)). Let 0g be the true parameter of interest, and 17 the true nuisance parameters governing the catargener process. For any regular, consistent, and asymptotically linear estimator & of 6o there exists function 3 called the influence function such that we decompose the estimation error Og using the von Mises expansion as:
θ 0g (Pn (O Gu nu) P (o; n) (0; nU)] (f)
M
Ma(
where Ply no)] = 0 (Tsiatis, 2006; Kennedy, 2016). Here, (i) the first term, M1, represents sampling variability resulting in asymptotic variance capturing the first-order behavior of Ô and reflects its asymptotic linearity (Ichimura and Newey, 2022: Kennedy, 2016); (ii) the second term, M2(f)). captures bias due to finite sample estimation of nuisance functions; (iii) the third term, Ms(fi). accounts for remaining higher-order approximation error that converges to 0 in probability at rate faster than vn.
By the Central Limit Theorem and the Slutsky theorem, the estimator is asymptotically normal (provided Donsker condition holds sample splitting is used):
vū( - 0g) ./' (0, Blp no) (O; (1))))))))
The asymptotic variance of Ô is thus determined by the variance of the influence function and can be consistently estimated via the empirical variance of the estimated influence function, v
Efficient Inffuence Function. The inffuence function depends the values of 0 and n) although we suppress this dependency for notational convenience. Among all influence functions corresponding to regular, asymptotically linear estimators of 6,, the efficient influence function (EIF), denoted 2b", achieves the smallest possible asymptotic variance. This minimal variance known as the semiparametric efficiency bound is given by: TE (O; fo. no) (O:6g, 11o) and represents the best achievable precision for unbiased estimation (Tsiatis, 2006; Newey, 1990).
Procedure Derive EIE. Consider the log likelihood L(O; 17) of observed data with parameter of interest 0 and nuisance parameters 7), maximized at (6., no). We define the score functions with
respect to 0 and as Ro(O;0, no) = ac 0o, '/o and R, (O; 0o, v0) = ac 39
Oo, V/o respectively. Ra Dij
reflects the sensitivity of the likelihood to 6. However, it may also be sensitive to r7. Projecting orthogonally to the space spanned by R,, isolates the component of information unique to 6. The efficient score function is the residual of Rs after projecting out components in the linear span of R,;
R' (O; 0o mo) Rg 11( [R An))
Herre P.)()) denotes the empirical average and p( the population expectation. The notation (v) shorthand for (v)) P(v). commonly used in semiparametric theory.

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where (( = [ [E R. and arguments (O; 00 77) suppressed for
brevity. The efficient influence function is given by v/* { [ -1 R² This influence function achieves the semiparametric efficiency bound and serves as the optimal estimating function for 0 under the given model. For further discussion and derivation, refer readers to Tsiatis (2006).
4 Data Integration with Disparate Outcome Measures
To leverage auxiliary data for estimating treatment effects on the primary outcome Y, we must establish relationship between Y and the auxiliary outcome W. We posit the following structural assumption that provides a foundation or "license" - for incorporating W into the analysis:
A.5. (Outcome Link Assumption) For all x and f. there exist functions a and / of pre-treatment covariates such that v (z) ( (x) + (1x)
Remark 1 (On Assumption A.5.). The assumption allows for flexible and heterogeneous relationships between primary and auxiliary outcomes across units with different values of X. However, this assumption also imposes structural restrictions on the relationship: the primary outcome is partially linear function of the auxiliary outcome W,, with the scaling factor (XX) and shift ((X) modulated by pre-treatment covariates X.
This assumption plausible in settings where W serves as a meaningful proxy for Y. For instance, in biomedical studies, W might represent surrogate endpoint (e.g., biomarker) that reflects the underlying disease progression captured by Y (Weir and Walley, 2006). In such cases, prior studies or mechanistic understanding can inform how changes in W relate to changes in Y.
4.1 Assumption Sets on (xX) and ((X)
To explore the range of identifiability and efficiency in leveraging auxiliary data, we consider three increasingly weaker assumptions about prior knowledge about (xX) and (
A.5(a) Fully Known Link: Both (xX) and ((X) are known from prior domain knowledge.
A.5(b) Partially Known Link: Only ((X) is known; aXX) is unknown.
A.5(c) Unknown Link: Neither (X) nor ((X) are known.
Assumption A.)(a) represents the strongest assumption, and is most tenable in domains with well- characterized mechanistic knowledge - such as certain areas of biology, pharmacology, or engineering where a(X) and ((X) are grounded in empirical studies or physical theory (Puniya al., 2018; Parikh et al., 2023a). In such contexts, auxiliary outcomes can be confidently incorporated using known mappings the primary outcome. Assumption A.b( relaxes this requirement by assuming only the baseline shift ((X) is known. This is common in applications where historical data or expert knowledge informs baseline trends, but the strength of association (i.e., scaling) between Y and W varies across populations or settings. Such partial knowledge arises frequently in social sciences or public health (Handelsman al., 1987). Assumption A.5(c)) is the most general and aligns with many real-world scenarios where no prior information is available about the relationship between Y and W. This assumption allows maximum flexibility, but also introduces the greatest challenge using an auxiliary study.
These assumptions represent a spectrum of tradeoffs between realism and statistical precision. Stronger assumptions enable tighter and more efficient estimation but rely more heavily on prior knowledge. We make this tradeoff explicit in Sections 4.2, 4.3 and 4.4. Ultimately, the appropriate assumption set depends on the context and credibility of available domain knowledge.
Function Class Complexity Assumption. We make additional assumptions about the complexity of functions in A.S.:
A.6. There exists positive constants 8 > such that A and B satisfies the covering number bound: log [(e, A. II) O(g-*a), and log ((e, II) O(.-wa). Further, we assume that the function class for jy and pw - -M- satisfies covering number bounds: log (e, [I) = O(E=M), with Wa Wg w.
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This assumption imposes regularity conditions on the function classes involved in the decomposition of (X) into a(X) and (X)). Specifically, it ensures that the combined complexity of and 9. measured via covering number bounds, does not exceed that of Jyy. This is a mild and natural requirement: if the auxiliary outcome W is informative about Y, then the residual mapping captured by ((X) is expected to be simpler than modeling (X) directly. In this sense, Assumption A.6. reflects a form of functional regularization, where using a predictive surrogate reduces the effective complexity of the learning task.
4.2 Semiparametric Efficiency Bounds
Now, we derive the efficient bounds under each of the following three assumptions A.5(a), A.5(b), and A.5(c), and investigate if and when data integration yields semiparametric efficiency gains. Throughout this section, we assume that assumptions A. A.4. hold.
Recall (O; fo, 70) =
(O; (O; fo no) R (O; 80 no), and the semiparametrically efficient asymptotic variance (i.e., efficiency bound) is equal to [E[RC (O; 0o, (1o) RO; [1] }
we only present the efficient score function R in- stead of the EIF r²" However, note that deriving the EIF from Rs is straightforward in our context. In our case, P(O = o, 02 m) = P(X = P(S
X = P = | x, S P(V
T=t,X= 2, S s) and L();0,n) log P(O o; n)
First, we derive the efficiency bound for the semiparametrically efficient estimator that only uses the primary study. We use this result as a base case to compare the efficiency bounds for the data integration- based estimators. This efficiency bound akin to the one derived in (Robinson, 1988).
Theorem 1 (Efficiency bound using only primary data). Under assumptions A.1.-A.4., the efficient score function using only the primary study (S = 0) is Rg (O; fo 70) = (1 - S) Ao-
The corresponding asymptotic variance is V8 V0(X) (X) E A = 0, x] p(S = 0 x)) where
Ao ((V - (L -uT() 0)))
T (- X.0)
o
Now, we derive the efficiency bound that leverages auxiliary data under A.5(a). Theorem (Efficiency bound under known a(X) and ((X)). Under assumptions A.I.-A.4 and A.5(a), the efficient score function is:
(0;00.. = S. A1 + (1 - S) -o.
where
T T (x,11)
A = (a()(VV -xx ((X) - (X
The asymptotic variance is:
va(X) (E [ S 0, X p(S 01 x) E [ S= 1, p(S =1 =1
Corollary 1. Integrating primary and auxiliary data under assumption A.5(a) yields efficiency gain Le. v (X) < (X).
Next, we derive the efficiency score and the efficiency bound for case when A.5(b) holds.
Theorem 3 (Efficiency bound under known 3(X) only). Under assumptions A.I.-A.4 and A.5(b),
the efficient score function for ((X) and (XX) is:
S A. (1- (. (MXX))
((X)T-px(XX11) )
(O; 0, co. ap)
The corresponding asymptotic variance-covariana matrix is:
(X) (Coo) (X)
Covi. (x)) with V((x) (E[A S S=0,X(((==0 (x)
Ex(X) :- Cov
Corollary 2. The asymptotic variance of the efficient estimator of ((X) under assumption A.5(b)
equal to that under using primary data only: Vg(X) ()()). Thus, when a(X) is unknown, incorporating auxiliary data provides efficiency gain.

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Theorem 4 (Efficiency bound under unknown x(X) and B(X)). Under assumptions A.I.-A.4.
and A.5(c), the efficient score function is identical that Theorem 3: R2 Bo og. 176)
(O; 0o og., no). Therefore, the asymptotic variance for estimating ((X) remains: (% (x) (X).
Corollary 3. both ( and ((X) unknown, there no efficiency gains from using auxiliary data compared to using only primary data.
The proofs and results in Theorems to are a direct consequence of following the procedure to derive EIF described in Section and are provided in Appendix B.
4.3 ATE Estimation under A.5(a)
Now, we present the ATE estimation under assumption (a). We use the efficient score R guide
the estimation of 8g using the property that R (O; no)] = O. Recall, that (O; fo, 77) = SA1 + (1 - So. Assuming an unbiased and consistent estimate of the nuisance parameter f). solution to 1 Σ, (O;; 0, fi) - denoted by 0₂ an unbiased and consistent estimate of 0g. Let (B) = A (BB denote the residual of random variable A after regressing A on B. Then, the
estimator 0, is given by:
Ei ((1 81) fx (X,, + +S fw (X.
0,
07
a(X,))
Σ, (11 (1- (1)
(X, (x.)))
+ S, (X:)
BY
Misspecification Bias under A.5(a): We showed the efficiency bound under three varied assump- tions and our results highlighted that efficiency gain is only feasible under the strongest assumption. Now, investigate the cost of making the wrong assumption i.c. what happens if we assume A.)(a) but a is misspecified. Let a denote the true a and amms denote a misspecified a.
Theorem (Misspecification Bias). Under assumptions A. I. - A.4. and a misspecified A.5(a), the estimator, 0a biased where the bias is equal to E [B() S = 1], where
B(X) = E [
(Xmms(X) a (X)) ((X) =
(x)
4.4 Estimation under A.5(b) and A.5(c): Finite-Sample Gains
In cases when is unknown (i.e. A.5(b) and A.5(c)), it is not feasible to yield efficiency gains by leveraging auxiliary data. However, consider the estimator for ATE only using primary data
0n E.(1 (x, 5)
This estimator can be modified, under A.5., to use the auxiliary data to potentially have finite sample benefits. One natural approach to leveraging auxiliary data is the following two-stage estimator: in the first stage, we estimate the auxiliary regression μo (X, using the auxiliary data and we then use this estimated function to predict pw (X, 0) for units the primary data. In the second stage, we estimate jay as: ( 0) a(X) (X, 0) + 3(x) where
E[ [ S =
à, 3 E arg min 1 E,(1 - S,) - (X,, B(x))) The resulting fitted no function (Xy,((X,)) combines both sources of information and provides a data adaptive estimator of the conditional mean outcome in the primary population. This approach is akin to adjusting for the prognostic or benefit score along with the vector of covariates (Liao et al., 2025). Thus, the resulting estimator leveraging the auxiliary data is given as:
0, Σ, - S.)((((, (f)
- (F)1-s) 0)
Quantifying Finite-Sample Risk. Asymptotically, nuisance estimators i) belong to a Donsker class or are fit using sample splitting, the M2 and Mg vanishes asymptotically at a rate
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faster than vn. However, in finite samples, they contribute non-negligibly to estimation error. We focus on (2) = P(o(O; n) v0 no)), which depends on the ac- curacy of nuisance function estimates. For cross-fitted estimators, we have: [M2(r) Op (n-1/2 (llay pa I| jr + 0u || p Since the only difference between 60 and 8, lies in the choice of outcome regression, smaller | - joy || directly translates into precise estimates.
Theorem 6 (Error bound for jvy. Given assumptions A.I.-A.4., A.5(b), and A.6., the empirical errors for jyo and the two-stage estimator fuy,b are
( - z4n no
( 1--Th
+ (n1/no) 24w ))
|| 11:00-py:1- = =0
and llāys -y = op
no
--
J+m no
Finite Sample Gains. Theorem 6 demonstrates that one may not even achieve finite sample gains when leveraging auxiliary data. The two-stage estimator by,s can outperform the direct regression estimator fv,o only when certain structural and sample size conditions are met. Qualitatively, gains arise when leveraging the auxiliary data allow for decomposition of Jy (X) into less complex functions. Additionally, leveraging auxiliary data helps only if μw (X) can be estimated accurately that is, when the auxiliary sample size n1 is sufficiently large relative to the primary sample size nop. Importantly, when the auxiliary outcome W is highly predictive of the primary outcome Y that is, when Cov(Y, W X) is large- - the function juy (X) can be wall-approximated by pa (X) then the function (xX) captures only residual structure and tends to be significantly simpler than jy (X) itself, implying that the entropy exponent Wa is relatively much smaller than w.
Characterizing
T4E T+wG + (mo//1)) > < 1. The first Quantitatively, finite-sample improvement occurs when no term captures the gain from replacing the full function class My with a lower-complexity class A, and the second term reflects the accuracy of estimating μ/w( (w(() from the auxiliary data. Gains are most pronounced when Wa < w (i.e., (XX) is much simpler than Jy (X)) and when nı >> no (i.e., we have ample auxiliary data). Our characterization formally supports the intuition that structural assumptions and additional data may result in finite sample gains.
In summary, finite-sample efficiency gains from incorporating auxiliary data arise when the function (X), capturing the dependence between Y and W, is simpler to estimate than jy (X). In such cases, one may first estimate μw (X) using auxiliary data, and then use the combined data to estimate aX). However, the existence and extent of these gains depend on the relative complexity of the function classes and the sample sizes involved. As no increases, the benefit of this two-stage strategy diminishes, and asymptotically, both the direct and the auxiliary-based estimators converge the same efficiency.
5 Medication for Opioid Use Disorder and Withdrawal Symptoms
We apply our framework to compare the effectiveness of extended-release naltrexone (XR-NTX) and pagrenorphine-naloxon (BUP-NX) in reducing opioid withdrawal symptoms between 10 and 12 weeks after treatment initiation. We begin by describing the primary and auxiliary datasets and the causal quantity of interest, followed by estimates obtained under three approaches: (i) using only primary data, (ii) incorporating auxiliary data with known outcome linkage (Assumption A.5(a)), and (iii) incorporating auxiliary data under partial knowledge of the link (Assumption A.5(b)).
5.1 Data Description
Primary Study: XBOT Trial. The NIDA CTN-0051 (XBOT) trial was multisite study comparing extended-release naltrexone (XR-NTX) and buprenorphine-nalon
(BUP-NX) for opioid use disorder treatment (Lee et al., 2018). A total of 540 patients randomized 1:1 to receive either treatments over 24 weeks. We focus on the most severe withdrawal symptoms in the 4th week, measured by the Subjective Opiate Withdrawal Scale (SOWS) 16-item self-report instrument where patients rate each symptom from 0 to 4, reflecting subjective withdrawal experiences.
Auxiliary Study: POAT Study. The NIDA CTN-0030 (POATS) trial enrolled individuals de- pendent on prescription opioids for outpatient treatment using BUP-NX (Weiss et al., 201 1). Withdrawal symptoms were assessed using the Clinical Opiate Withdrawal Scale (COWS), an ll 11-item iimician-adminiseee tool capturing objective signs of withdrawal. We use POATS as
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auxiliary data to improve the estimation of withdrawal severity under BUP-NX in the XBOT trial, leveraging the worst COWS scores in the 4th week. Although the XT-NTX arm is absent in the auxiliary dataset, the BUP-NX treatment is shared across both studies. We aim to evaluate if and when auxiliary information on BUP-NX can be used to improve the efficiency of estimating the outcome under BUP-NX in the primary population, while carefully considering the assumptions required for valid data fusion.
5.2 Analysis
We evaluate the comparative effectiveness of XR-NTX (T = 1) versus BUP-NX (T' 0) in reducing withdrawal symptom severity, measured by the worst SOWS score in the fourth week (Y), among participants in the XBOT trial. In the auxiliary POAT study, withdrawal severity is measured on the COWS scale during the same period (W). We use common set of covariates assessed in both trials (X). Further, we only considered patients for whom we observed the outcomes - our study excluded individuals for whom treatment was not initiated or who dropped out before our outcome window.
To harmonize the two scales, we derive the transformation coefficient a from published clinical thresholds. According to Wesson and Ling (2003), COWS ranges of 5-12, 13-24, 25-36, and >36 correspond to mild, moderate, moderately severe, and severe withdrawal, respectively. Similarly, Handelsman et al. (1987) defines SOWS ranges of 1-10, 11-15, 10-20, and 21-30 for the same categories. Assuming both scales share a zero point (no withdrawal). we align category midpoints and estimate linear mapping Y = oW + e, yielding visualizes this relationship. We assume a is constant across covariate values X, and interpret lower values of both Y and W as indicating better outcomes. We then apply the three estimators introduced in Section 4.3 and 4.4: Og (primary data only), Ó, (auxiliary data, unknown o)), and 0₂ (auxiliary data, known a). As shown in Figure (bb), Og and 6, suggest that XR-NTX and BUP-NX are almost equally effective. However, 0, suggests BUP-NX is marginally more effective lowering withdrawal symptoms compared to XR-NTX. Specifically: (i) 6 = -0.18 (95% CI width: 1.52), (ii) 0 = 0.42 (95% CI width: 0.65), and (iii) 0,- - -1.08 (95% CI width: 1.41). While O, achieves a statistically significant result, it relies on the correctness of the assumed a. To assess robustness, we conduct sensitivity analysis by varying a within +500 of the estimated value, i.e., E [0.31, 0.92], assuming the linear form remains valid. Figure Icc) displays the resulting 6, estimates across this range. Although the point estimates vary - from 0.50 to 0.33 - they consistently favor BUP-NX over XR-NTX. However, for a > 0.75, the 95% confidence intervals include zero.
0.61 and intercept 3 = 0. Figure (a)
Takeaways. In our case study, assess whether XT-NTX is more effective than BUP-NX in reducing withdrawal symptom severity. The point estimates from the primary study are slightly negative, suggesting a marginal advantage for XT-NTX, but the 95% confidence interval includes zero, indicating no statistically significant difference between the two treatments (see Figure 1(b); estimate 6g). To improve estimation precision, we explore leveraging auxiliary data. Under the strong assumption, our combined analysis yields a statistically significant result favoring BUP-NX over XT-NTX (see Figure 1(b); estimate 0z). While such findings may appear actionable, they hinge critically an untestable assumption linking outcomes Y and W. If this assumption is violated, the resulting estimates may be misleadingly precise. Our case study thus serves as a cautionary example: although integrating auxiliary data can improve precision, it must be done with scrutiny of the underlying assumptions, which- if invalid can lead to confidently incorrect conclusions.
Discussion & Conclusion
Summary. This paper presents principled framework for integrating primary and auxiliary datasets with non-overlapping, disparate outcomes improve efficiency in causal effect estimation. We focus on settings where the primary outcome is never jointly observed with the auxiliary outcome, and we introduce a structural assumption that links the two. Building on this, we define three scenarios reflecting varying levels of prior knowledge about outcome relationship and derive semiparametric efficiency bounds under each. Our findings show that efficiency gains are guaranteed only under the strongest assumptions, when the linking equation is fully known. In contrast, under weaker assumptions, asymptotic efficiency not ensured. However, finite-sample improvements are still possible, particularly when the auxiliary outcome is highly predictive of the primary outcome. These

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28
Plot 6.
Theatment Effect (as mmsasuuee on SOWS)
0.75
0.50
-0.18
0.25
-0.5
-1.0
0.6
0.8
8
DOWS
(a)
(b)
(c)
Figure 1: MOUD Results. (a) Scatter plot showing the relationship between SOWS and COWS. (b) Treatment effect estimates of MOUD on withdrawal symptoms. Point estimates and corresponding 95% confidence intervals for da Oa and 6g. (c) Assessing the sensitivity 0a to the different values of in the range 50% above and below the original guess of 0.61.
benefits taper off the primary sample size increases, highlighting the limitations of auxiliary data in isolation. We support our theoretical results with both simulations and a case study estimating the effect of medications for opioid use disorder (MOUD) withdrawal severity. Here, combine data from the XBOT trial (SOWS scale) and the POAT study (COWS scale), demonstrating the framework's practical utility.
Limitations & Future works. Our analysis and results in this paper depend on the structural assumption between Y and W. While moving ahead, we will focus making our results more general by relaxing this assumption; it is important to note that the lack of efficiency gains restrictive context would imply similar conclusion in more complex context. Further, will focus on incorporating a third "bridge" dataset, where both outcomes are observed, which could help relax strong assumptions and expand the conditions under which efficiency gains possible. We will also explore relaxing the assumption of conditional study exchangeability, extending the framework to accommodate discordance in treatments and covariates across studies. Further, framework requires that at least one treatment arm be shared across the primary and auxiliary studies. When there is no treatment overlap between datasets and the outcomes vary from one study another, becomes impossible to link the potential outcome distributions. This makes it difficult to use auxiliary data to enhance efficiency gains. This situation reveals a significant structural limitation in data fusion settings. In the future, we plan to explore data fusion in such scenarios by imposing distance metric to the treatment space, which will enable compare different treatments.
Acknowledgments
The authors would like to thank the reviewers, the area chair, and the program chair of NeurIPS 2025 for their constructive input to help improve the paper. Further, Harsh Parikh, Kara Rudolph, and Eliz- abeth Stuart would like to acknowledge that this work was funded by NIH NIDA ROIDA056407, and Caleb Miles and Kara Rudolph would like acknowledge that this work funded by NIH NIDA R01DA059824. Trang Nguyen and Elizabeth Stuart were funded by NIH NIMH RO1 MH126856.
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Answer: [Yes]
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Question:
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Question: Does the paper fully disclose all the information needed to reproduce the main ex- perimental results the paper to the extent that affects the main claims and/or conclusions of the paper (regardless of whether the code and data are provided or not)?
Answer: [Yes]
Justification: We provide all the details of our real data study in Section 5 and simulation study in Appendix.
5. Open access to data and code
Question: Does the paper provide open access to the data and code, with sufficient instruc- tions to faithfully reproduce the main experimental results, described in the supplemental material?
Answer: [Yes]
Justification:
The
data is publicly
available and
at
(i)
XBOT:
https://datashare.nikk. www..nii...pppmmmmmmmmmmm www..ni..ooossuudyiidaaac----oee
(ii)
POATS:
https://datashare..iin wnw.e.nniaiiiii. www........../aiiii.e htw.aaiiw../ossuddiidaaaa------- Combined
CTN0094
data is
also available here: https://gihbbbbooomm/ccc//////pp
6. Experimental setting/details
Question: Does the paper specify all the training and test details (e.g., data splits, hyper- parameters, how they were chosen, type of optimizer, etc.) necessary to understand the results?
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Justification: Yes provide all implementational details our approach in the paper. As well as attach code in the supplementary material section.
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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: Our results show appropriate uncertainty quantification and 95% confidence intervals in Figure 1. Our results also provide asymptotic variance quantification for our
estimator.
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Appendix A Synthetic Data Study and Results
In this section, we are interested in understanding the performance of estimators under various sets of assumptions (a.5(a) to A.)(c)). In particular, we interested in understanding the potential gains as (i) total number of units, n, increases, (ii) the dimensionality of X, denoted as increases and (iii) the log of the ratio of number of units the auxiliary to primary dataset, log First, we discuss our data generative procedures, and then present and discuss our results.
P(S=1) increases.
((s=0)
Data Generative Procedure. The data generation procedure (DGP) in this study is designed to
simulate complex causal structure. We begin by generating covariates X (X1, X2, Xp)) from a multivariate normal distribution with zero mean and identity covariance matrix where p is the number of covariates. The binary study indicator S is then generated as a Bernoulli random variable, where the probability of assignment to the auxiliary study (i.e., S = 1) is Pr(S = X) = expit( + a1 X1 + X2), where expit(x)) I=c-r- The treatment assignment T is also generated as a study and covariate-dependen Bernoulli variable Pr(7' 1|x, S) (1 S) 0.5 + S expit((1-X1).
The auxiliary outcome W, observed only in the auxiliary study (S = 1), is defined as follows:
W pw T,, + (70 X1 (2) T 81 82 + 83X3 30
where vectors 7 and 3 define the treatment and baseline effects on W. This equation includes both linear and interaction terms, capturing treatment-covariate dependencies. In the primary study (where $ = 0), the primary outcome is modeled as: Y = ((X) (X,,T, (X, +y where (XX) = P1 + Pu- This outcome depends the treatment effect modulated by covariate-driven heterogeneity in (XX), capturing treatment- treatment-mediated effects of covariates on Y.
Here the true ATE in primary is given as 0p E [(Po + 11X (no + x + (2X)) S = 0].
Analysis and Results. We use mean-squared error (MSF) to compare the performance of the following three estimators: (i) efficient estimator only using primary data (0o). (ii) efficient estimator augmented with auxiliary score (f,) and (iii) efficient estimator with known a integrating auxiliary data (0.). The simulation results are compiled in Figure 2. As expected, the performance of all increases. Further, d, dominates d and 0, especially for scenarios with large p and/or large log P(S==)) indicating that scenarios where the primary study is relatively small and the problem is high-dimensionn
three estimators improves
increases and deteriorates
P(S=0)
leveraging auxiliary data yields more benefits. This aligns with our theoretical results showing that knowing a can yield efficiency gains. For, 0, (which uses auxiliary data), we observe that it yields benefits relative to 0 in small n scenarios especially when p and log
P(S=1) are large. However, these benefits diminish P(S=D))
relative to 6g as n grows. This is consistent with our theoretical result showing that there are no asymptotic benefits if a is unknown. However, there are some finite sample benefits of using the auxiliary score even when is unknown.
Appendix B Efficiency Score Functions Derivation (Theorems 1-4)
derive the EIFs and correspond- ing efficiency bounds under the three sets of assumptions. As (O; 0g %)) [E[RR (O; (0 R² (O; (o)(o.n)))=]> RO; no), and the semiparametrrcally efficient asymp- R (O; Oo "m]= we only totic variance (i.e., efficiency bound) is equal to [E; 0o. RR
Following the above mentioned procedure
present the efficient score function R instead of the EIF vla". However, note that deriving the EIF from R' is straightforward in our context.
16

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p-5 and log
(15=01
(15=11
1-000
p-10 and log /3=00)
(3-1)
1-0.0
p-20 and log) solns-wp) [1t==1)
(15-0]
|-0.0
Estimato
0.00125
0.0000
0.01000
6,
0,00100
0.00378
6
0.0011
0.00075
MSE
0,00000
6
0,00000
0.0010
0.00025
0.0006
0.00000
0,00000
0.0000
p=5 and log (1
F1.0
p=10 and log
(855
F1.0
p-20 and log) R[
=1.0
0.003
0.003
0,002
199
0.002
0.001
0,000
0.000
0.000
pa5 and log
RSS
R3
|2000
p=10 and Ing 23-00
(S5
$200
p=20 and log
[SS
-2.0
0.0126
0.015
0.0100
0.020
0.0375
0.010
0.018
0.0050
0,010
0.005
0.0328
0.006
0.0000
0.000
0.000
500
1000
2000
500
1000
2000
500
1000
2000
Figure 2: Simulation Study Results. Mean squared error rates for three different estimators d. 6g and 0g based on Ry. Ry and Ri
In case, 0 (X,S,T.V), P(O x, S = =
x P) X = T and and 10000:0000000000000000:000000000 Thus,
L(0:0, 1) = logP(X = z) +
= = =
+ +lggP(V = T
-lopP(X = x) (og(Sys(z)+( +1 -)) - ps(#)))
+ (log(TwT(z,s)
+ +log(P(V==)) = T T
We know that V SW (1- and Y = o(X)W + B(X) +
Thus.
= =
=
Simplifying further,
P(V T S X r) (1 T -,
Substituting Y with (XX) + 9(X) +
P(V = -
=:hh=:"""h(lll.......kk("::",,,3 =x)
= -sP(y-c=a(x)
+(1 - -1--::1((00000000000000220011110
-
sP((a(X) -=hh:--wwkkk)))00000---0011----0
+(1 P( (o--,(1000000000000xxdd00-11-3--
=P(0 (v /x(111)) ((X) (T (
a(X)
(1 P)P (v (n- (u-xy(X,0) (T)) (X( T = = z).
T
17

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Assuming and å are normally distributed with mean 0 and homoskedastic variances of and 03 respectively,
logP(V
= = = x
(ix) (- ((e-pw(
(t- (t-pr (t-
8 sexp
2 (le-py (x.0))
-log
+(1 8) exp
(c.00))0((a)))) ((x)( (
20
Efficient score function using only primary data (Result of Theorem 1). Now, we first show the efficient score function for the case that only uses primary data. This works as a baseline case for us and the subsequent efficiency bounds are compared with this case. The efficient score function under assumptions A.2. and A.4. is given as:
R5; 0o no) ()- ((V (0y--r((X0)) 0)) - ((X) ur 0))) (T- Ur
o3
Let Do
then E (O; 0o (R,(; fo no))² = E [(1 - -5) and the asymptotic variance xx(x)= = (E [(R](O; fo (R) (O; (u.0;u..0 mo)) mT) = E S 0, p(S = X)
((VV-py (X, - (T 0))) (T-r(XX0)
Efficient score function under assumptions A.1.-A.4. and A.5(a) (Result of Theorem 2). Under this assumption, only 0 is unknown and would be estimated using the data while and 33 are known a priori. Thus, the efficient score function under A.)(a) is:
- (T(X, -x- S. ((a(x)(V - ww((, 1)) - (( ( ((1- ((CV- - -X, 0)) - ((X))(T-Tr(X -x((X)))) (2-vr(X_0) -
R (2; no) =
a²(X)o?
Let A1 = ((a(x)(V-Aw(X (x, - (T - (xx, (T-Mr(X.1)) Then, the asymp-
totic variance
E A
S 0, p(S =0 x) S 1,X pls = X)
(x)x= (B(R) mo) (O; 0o no))² x)) x1))
+E A
V2 is always smaller than or equal to (X) because E non-negative.
A
S = 1, pls = 1 X) is
Efficient score function under assumptions A.1.-A.4. and A.5(b) (Result of Theorem 3). Here, along with 0, a is an unknown parameter. Thus, the efficient score function is given as:
Hw (X. S ((cx - ((x)
(X), -r((0))))
(T-pr(X.1)
++11 (+())- (1(1-5)) 5). (((V - (x, ((X)
a² (X)o
Rg (O; (fo, ao0. n0)= =
(T- S. (xX)) -W (())
a=(X)o
a(X)
B((R)(R)))) | X| = (
[SA (1 - -)40
)
(SA + +1- #(X)
a(x) -XX)5A)) SA,)
)
8(x) SA
a(x)
/E|A x = 1) = + E X,S = -
((X)
E B[A X,S 1|S=11
((x) x(X)
E|A X,S = P] = x
(x(x)
E A
X,S =
xxx
The asymptotic variance-covariance is then
=(mm(x (x)
Coug 0.a (X)
Ex(X) = (Cou (X) (X)
= (B |x)) -1
(X)
xo(X)
BANX -- O|)=
Tx1 S
xx (x)
[o(X))
[o(x)
(AANIX.==0P(S=00)
EA X.S=IIJP(SSIIXX)
18

---

From this, we see that the asymptotic variance for the efficient estimator of 8 is (g(X) S=0PS Note, that this asymptotic variance (g( = (d()). This highlights that under assumption (b) there are no efficiency gains from leveraging auxiliary data compared to the baseline which only uses the primary study.
Efficient score function under assumptions A.1.-A.4. and A.5(c) (Result of Theorem 4) As the likelihood is agnostic of 3, the efficient score function under A.5(c) is identical to that of A.5(b),
i.c.
(O; (0o, ao). no) = (O; 100, ao). mo)
As the score functions are identical under assumptions A.)(b) and A.5(c), the asymptotic variance S is also identical. This indicates that there are no efficiency gains from leveraging auxiliary data compared to the baseline that uses only the primary study.
Appendix C Proof of Theorem 5 (Misspecification Bias)
Proof of Theorem 5. We begin by defining 6, as the estimator solving the empirical moment condi-
tion R, (O; 0.. f)) = O. In the population, 6o solves ( 00 no)] = 0 only under the correct specification of a = a*. We now investigate what happens when the analyst assumes a = Omiss
where a'mis # a". Recall, 0g is
Σ, (1 11-S S,) (x) (X..))
SS (X.
a(x.)
Σx (1 S:) (),
+ S
(X.11.11
(X.)o
Thus, (Amis)) 0a [a*)] EiOa (aimss) (a))
) S P 0) (amis) - (a
S I]P(S 1). In the estimator, terms with (1 5) do not interact with a. Thus, E (0lia))
(a(a') 1 = 0) O. Now, consider R (ammis) (a())) s = P(S = 1).
El0a(amis)) - (aaaa) |5 = 1] =
E EE Oa (Amis) - (a(a') =
El0g(0misd) Oa(a') Xx5 = 1] (Omis (X) a² (
(Fw (X. (X,1)rr(X11) (E (X, 1)))
X, S
(amis (X) a² (X)) (X) 1)]
|X,S =
(x) (Uiis (X) a² (X))
(X1 1)))
((X) x,S=
(X)
Appendix D Proof of Theorem 6 (Error bound for j
Proof. We analyze the estimation error for both juyo and jas under the given metric entropy assumptions.
(i) One-stage estimator joy:0- By assumption A.6., by E M, and the metric entropy of M satisfies log N(,, || II) S CW
From standard results in empirical process theory and nonparametric regression (e.g., Györfi et al. (2006) and Tsybakov and Tsybakov (2009)), it follows that the least-squares estimator fiy; satisfies
|l - ny = =0p nno (mo 1/((tw))
19

---

(ii) Two-stage estimator Py.- By assumption A.5., JY (X) a a(X) (X) ((X). We estimate
Aw (X) from ny auxiliary samples. Let füw be an estimator satisfying
V/w pw = 0p (n) (
under the assumption that μw M and satisfies the same entropy bound as jay The two-stage estimator is defined as:
(y,(X) a(X) fow (X, + 3(X),
where (á, B) minimize the squared error loss over the primary sample:
1 no
(á, B) arg min a'A, BEB nio
Σ (Y; ((X))xw -x(xx
We now decompose the error:
M My = llaj + apw -B1--
Adding and subtracting intermediate terms:
(I( - a)jw + ae(iw - pw) + (B -3]1--
Applying triangle inequality:
|yA - pyll < lI(à - awlll ao + ||a]|lo - #w)ll + ||3 B|1.
Under the assumption that fo is uniformly bounded (which holds if μw and faw are bounded and consistent), and using the entropy conditions on AA and B:
|| all (1 -1/(2t0)) (given A.6.), and,
|| 311 = 0 (given A.5(b))
Combining all the pieces, we obtain:
-1/(2-w)
I uy = op T10
-1/(2t+
110
Slwa
71
Yin
where the first term reflects the complexity reduction from modeling Jy via ((X), and the second term reflects the error propagated from estimating μw using auxiliary data.
20


Reviews:
[{"review_id": "uL7MnqDO1Y", "reviewer": "Reviewer_BAwh", "summary": "Experimental studies often have low population sizes, so it would be beneficial to be use all of the data to draw conclusions about treatment effect.  However, one potential pitfall is that there may be multiple ways to measure a given outcome.  If these measures are not simple transformations of each other (e.g., Fahrenheit vs Celsius), it's less straightforward to use the results from one population to aid in drawing conclusions about the other, and, if the mapping is complex/opaque enough, there may not be any benefit at all.  The authors explore the situations in which such generalization can be done.  They break down three assumption sets based on the level of knowledge about the mapping and give clear descriptions of when using information from a secondary population would be useful.  They present results from a pair of empriical studies to show how their approach can be used in practice.", "questions": "It's possible I'm missing something, but I'm not following the terminology in the Influence Function section (the equation after line 145).  In Section 3, you defined $P_n(f(A))$ as the average and $P(f(A))$ as the population average of some function $f$.  However, in this equation, we see $P_n$ and $P$ with no function.  Unless there was some statement that I missed about what they mean standalone, I'm not sure how to interpret $(P_n - P)$ at the beginning of that equation.\n\nAs I noted under Strengths and Weaknesses, it seems as though the XBOT and POAT studies have different treatment definitions.  Is this correct?  If so, does that mismatch introduce any issues?", "limitations": "Yes, I believe the authors discussed the limitations sufficiently", "rating": 5, "confidence": 3, "soundness": null, "presentation": null, "contribution": null, "strengths": "", "weaknesses": "", "quality": 3, "clarity": 2, "significance": 4, "originality": 4, "strengths_and_weaknesses": "I think the problem that this paper is tackling is an important one, and I think the way the way the authors tackle it (showing the utility as assumptions strengthen) is compelling.  Ultimately, I think this is a good paper, though there are some clarity issues that could be improved.  I would be happy to increase my score if these issues are addressed and my questions are answers.\n\nFrom Section 3, it sounds like the assumption is that the treatment and covariates are the same between the two studies and that the outcome is the only piece that's allowed to differ in definition/measure.  However, looking at the two studies used for the experimental results, I'm not seeing this assumption being met.  It looks like for the XBOT trial, treatment is XR-NTX vs BUP-NX, while for the POAT study, treatment is BUP-NX vs BUP-NX with counseling.  So while both have BUP-NX as one of the treatment values, the other value seems to be non-trivially different.  They also seem to have different treatment schedules.  It's very possible I'm missing something here, but if not, it's strange to not mention this when it seems to violate an assumption of your approach.\n\nThe experimental results are interesting, but I could use another sentence or two of analysis.  From this, would you conclude that the studies show that BUP-NX is likely more effective than XR-NTX?  Does this suggest any future avenues of study, or that additional data should be collected?  It's almost there, but with the conclusion stating that the experiments \"[demonstrate] the framework's practical utility\", some mentions of the actual practical takeaways would help.\n\nIf you're going to list simulation study results as one of your contributions, it would be helpful to at last include a short summary of the takeaways from those experiments in the main paper.  As it is, it's strange that they're not mentioned outside of stating their existence in the introduction and conclusion.\n\nSections 4.3 and 4.4 seem to be where you do the main summarizing of your results.  However, I think a higher level summary before going into Section 5, making it very clear what the key takeaways are and what the conditions are that allow for any gains from using the second population, would aid with clarity.", "was_revised": true, "final_justification": "Ultimately, I think this paper is a valuable contribution.  Especially in fields or specific problems with sparser data availability, it makes sense that people would want to combine study results, and I think this paper takes a very cautious and reasonable approach to addressing this.  I especially like the fact that the takeaway is not just \"Here's a fancy new method for integrating study results\" but rather \"You can integrate study results, but only if you're willing to make some pretty strong assumptions that may not hold in practice.\"  This sort of science - exploring the limits and assumptions around when you /can't/ do something - can be incredibly valuable to the community, and I think this paper is worth publishing for that reason.  There are some clarity concerns from other reviewers that I hope the authors address, but nothing that I feel is fatal.", "rebuttal": "We sincerely thank the reviewer for their thoughtful and constructive comments. Below, we address the key concerns raised and summarize the corresponding updates made to the manuscript:\n\n**1. Clarifying the Use of Auxiliary Data Despite the Absence of XT-NTX**\n\nThank you for this thoughtful and nuanced observation. You are absolutely right—the XT-NTX arm is not present in the auxiliary study. However, since BUP-NX is common to both the primary and auxiliary datasets, our goal is to assess whether and under what conditions information on BUP-NX from the auxiliary study can be leveraged to improve the efficiency of estimating $\\mathbb{E}[Y(t=\\text{BUP-NX}) \\mid S=0]$ in the primary study population. We have revised the manuscript to clarify this point. The updated text reads:\n\n> *“Although the XT-NTX arm is absent in the auxiliary dataset, the BUP-NX treatment is shared across both studies. We aim to evaluate if and when information on outcome response to BUP-NX from auxiliary study can be used to improve the efficiency of estimating the outcome under BUP-NX in the primary population, $\\mathbb{E}[Y(t=\\text{BUP-NX}) \\mid S=0]$, while carefully considering the assumptions required for valid data fusion.”*\n\n**2. Main Takeaways from the Case Study**\n\nThank you so much. We have added the following to describe the main takeaways of our case study:\n\n> *“In our case study, we assess whether XT-NTX is more effective than BUP-NX in reducing withdrawal symptom severity. The point estimate from the primary study is slightly negative, suggesting a marginal advantage for XT-NTX, but the 95% confidence interval includes zero, indicating no statistically significant difference between the two treatments (see Figure 1(b); estimate $\\hat{\\theta}_0$). To improve estimation precision, we explore leveraging auxiliary data. Under the strong assumption, our combined analysis yields a statistically significant result favoring BUP-NX over XT-NTX (see Figure 1(b); estimate $\\hat{\\theta}_a$). While such findings may appear actionable, they hinge critically on an untestable assumption linking outcomes $Y$ and $W$. If this assumption is violated, the resulting estimates may be misleadingly precise. Our case study thus serves as a cautionary example: although integrating auxiliary data can improve precision, it must be done with careful scrutiny of the underlying assumptions, which—if invalid—can lead to confidently incorrect conclusions.”*\n\n**3. Placement of the Simulation Study**\n\nThank you so much for your helpful suggestion. Due to space constraints, we initially moved the simulation studies to the appendix. However, following your recommendation—and now having an extra page available for the camera-ready version—we have moved the simulation study back into the main text. We believe this change strengthens the paper by making the empirical insights more accessible and better integrated with the theoretical results.\n\n**4. Summary of Theoretical Takeaways**\n\nThank you so much for the extremely constructive input. We have added **Subsection 4.5**, which summarizes the main theoretical and technical takeaways from our results.\n\n**5. Clarifying Notation: $(P_n - P)(\\psi)$**\n\nThank you for the question. The expression $(P_n - P)(\\psi)$ denotes the difference between the empirical average $P_n(\\psi)$ and the population expectation $P(\\psi)$ of the influence function $\\psi$. This is a standard shorthand in semiparametric statistics and causal inference literature, used frequently to express asymptotic linearity and derive variance for regular estimators (see, for example, Kennedy 2016; Tsiatis 2006). To avoid confusion, we have clarified the notation in the revised manuscript. The updated text reads:\n\n> *“Here, $P_n(\\psi)$ denotes the empirical average and $P(\\psi)$ the population expectation. The notation $(P_n - P)(\\psi)$ is shorthand for $P_n(\\psi) - P(\\psi)$, as commonly used in semiparametric theory.”*\n\n**6. Necessity of Shared Treatment**\n\nThank you for raising this important point. The goal of our paper is to understand whether, and under what assumptions, auxiliary data can be used to improve efficiency when the outcomes differ across studies. In this context, at least one treatment arm must be shared between the primary and auxiliary studies. Without a common treatment and in the presence of disparate outcomes, it becomes fundamentally impossible to leverage auxiliary data for valid causal inference. We have updated the discussion section to clarify this point. The revised text reads:\n\n> *“Our framework requires that at least one treatment arm be shared across the primary and auxiliary studies. In the absence of such overlap, and when outcomes differ across studies, there is no basis for linking the potential outcome distributions across datasets, rendering auxiliary data less usable for improving efficiency gains. This highlights a key structural limitation in data fusion settings with disparate outcomes.”*"}, {"review_id": "8Wf4t0AWQ7", "reviewer": "Reviewer_Jw35", "summary": "The paper studies (conditional) treatment effect estimation in a setting with two distinct but related outcomes. The authors study the question whether data from an auxiliary study, whose outcome is given by a partially linear function of the main outcome, can lead to efficiency gains compared to only using data from the primary study. The authors introduce three sets of assumptions, from fully known to fully unknown (up to the partial linearity) link between the two outcomes. The main result of the paper is that semiparametric efficiency gains over using only primary data are only possible if the relationship between the two outcomes is fully known (Theorem 2, Assumption A.5(a)). Theorems 3 and 4 illustrate that as soon as the main link alpha is unknown, the asymptotic variance of both estimators is equal. However, the authors show that under the less strict assumptions A.5(b) and (c), finite-sample gains can still be observed, e.g., if the auxiliary outcome can be estimated accurately and  the amount of auxiliary data is large. The authors illustrate their theoretical findings via simulations and a pair of real-world medical studies with linked outcomes.", "questions": "1. Is it possible to extend Theorem 2 to a slightly more complex relationship between $Y$ and $W$ in Assumption A.5? For example, if the link is a known nonlinear function, e.g., $\\nu^t_Y(x) = \\alpha(x) (\\nu_W^t)^2(x) + \\beta(x)$ instead of linear, would the efficiency gains persist?\n2. The framework assumes that $\\alpha(x)$ and $\\beta(x)$ are deterministic functions. What would change if $\\alpha$ and $\\beta$ were instead random functions? Have you considered this case?\n3. What happens if under the same assumptions and knowledge of $\\alpha$ and $\\beta$, one wants to estimate the ATE/CATE for the auxiliary outcome $W$ instead of the main outcome $Y$? \n4. In Section 5.1, it is mentioned that the primary study consisted of 540 patients. How many individuals were enrolled in the auxiliary study?", "limitations": "The authors have properly addressed the limitations of the study.", "rating": 4, "confidence": 4, "soundness": null, "presentation": null, "contribution": null, "strengths": "", "weaknesses": "", "quality": 3, "clarity": 4, "significance": 4, "originality": 3, "strengths_and_weaknesses": "Strengths:\n1. The paper is very well-written, self-contained and logically organized. The assumptions are introduced and discussed incrementally. \n2. The theoretical results are well-formulated, the assumptions are clearly stated. Each result is supplemented with a qualitative discussion.\n3. The main insight, namely the limited usefulness of auxiliary data which only persists if the link function is fully known, is novel and interesting, i.a. as a tale/instruction to practitioners. \n4. The relevance of the introduced problem is clearly illustrated on the example of the XBOT trial and the POAT study. \n5. Good reproducibility via the provided code and experimental details.\n\nWeaknesses:\n1. The paper would greatly benefit from including the case mentioned in the discussion, namely estimating alpha from a \"bridge\" dataset, since the ground-truth link between the two outcomes (as assumed in the paper) cannot be known precisely in practice.\n2. In the synthetic simulations, it would be useful to see which effect a misspecified link function alpha has on the finite-sample results. Specifically, what is missing as an illustration of Theorem 6, is an empirical validation of how the bias scales with the $\\alpha$-estimation error, as well as a comparison of estimators under a misspecified $\\alpha$. \n3. Theorems 3 and 4 appear to be largely the same result, since they yield identical efficiency bounds. These could be merged into a single theorem to make the presentation more concise. \n4. The paper assumes a link between $Y$ and $W$ which is linear in $W$, which can be quite restrictive in practice. Additionally, it is not discussed whether this assumption is necessary for the theoretical results or whether a known nonlinear relationship could be explored.", "was_revised": true, "final_justification": "The authors addressed most of my concerns, adding simulations and clarifications. However, I still consider the extension to multiple confounders very narrow, and the empirical validation with real-world data is limited. I would thus like to keep my borderline positive score.", "rebuttal": "We sincerely thank the reviewer for their thoughtful and constructive feedback. We greatly appreciate the opportunity to revise our manuscript and have carefully addressed each of the concerns raised. Below, we summarize the key changes made in response to the reviewers’ comments and questions:\n\n---\n\n### 1. Lack of a “bridge” dataset with both outcomes (COWS and SOWS)\n\n We agree that including a dataset in which both outcomes are simultaneously measured would significantly strengthen the empirical component of the paper. However, to the best of our knowledge, no such dataset currently exists for the MOUD case study. Importantly, one of the key prospective implications of our work is to motivate the design of future studies that collect both outcomes in tandem, enabling more assumption-lean data integration. We have added a discussion of this point in the revised manuscript.\n\n---\n\n### 2. Simulation study exploring bias due to misspecification of $\\alpha$\n\n In response to the reviewer’s suggestion, we added a new simulation study to examine the bias introduced when $\\alpha(X)$ is misspecified. The simulation results closely align with our theoretical findings and serve to further motivate the cautionary conclusions drawn from our real data case study. This addition reinforces the broader message that violations of the assumptions underlying data integration can lead to bias.\n\n---\n\n### 3. Merging of Theorems 3 and 4\n \nWe agree that merging these results improves clarity and conciseness. We have accordingly updated the manuscript to reflect this revision.\n\n--- \n\n### 4. Generalizing the relationship between Y and W\n\n Our original results were derived under a partial linear assumption: conditional on X, Y and W are linearly dependent. This assumption was chosen for clarity and parsimony. However, as suggested, we have extended our analysis to a more flexible setting where: $Y = \\alpha(X) \\cdot \\zeta(W) + \\beta(X) + \\text{noise}$\nwith $\\zeta$ being an arbitrary (possibly nonlinear) function. Our analysis shows that efficiency gains are only achievable when both $\\alpha(X)$ and $\\zeta(W)$ are known, consistent with our original conclusion. This generalization strengthens our central message: efficiency gains through data integration are only possible under strong, often untestable, assumptions about the relationship between outcomes.\n\n---\n\n### 5. Additional theoretical considerations\n\n We have clarified that our paper does not address the case where \\alpha and \\beta are random functions. We view this extension as outside the current scope and have noted it as a limitation and potential direction for future research. We believe that relaxing this assumption would only further constrain the potential for efficiency gains under even the strongest conditions.\n\n---\n\n### 6. Interpretation of “primary” vs. “auxiliary” data labels\n We appreciate the reviewer’s question regarding the asymmetry between primary and auxiliary datasets. We clarify in the revised manuscript that these labels are somewhat arbitrary and the framework is symmetric in structure.\n\n---\n\n### 7. Clarification on the sample size of the auxiliary dataset\n The auxiliary dataset used in our case study contains 324 individuals. We have now explicitly clarified this in the main text to avoid confusion.\n\n---\n\nWe are grateful for the opportunity to revise our work and believe that these changes have significantly strengthened the manuscript. We hope the revised version addresses the reviewers' concerns and communicates the contribution of our work."}, {"review_id": "vkwj9jXTIP", "reviewer": "Reviewer_ScZv", "summary": "In the paper, the authors considers the data integration problem where the two studies have different outcomes. \nTo put it in a simpler way, one study has the outcome but the other only has the surrogate outcome.\nThe authors introduces different modeling assumptions and the assumptions between the two studies, and mainly studies whether and when integrating such studies lead to benefits.", "questions": "The structural models (1) and (2) considered in this paper seem quite restrictive. They indicate that normal errors and the difference between the two potential outcomes are a deterministic function of X, not random. I’m quite curious what the overall story of this paper would change if the authors do not assume this assumption.\n\nAlso, in (1) and (2), are \\sigma^2_Y and \\sigma^2_W known or unknown? If unknown, how to estimate them and how would they affect the efficiency bound?\n\nThe assumption A5 also seems quite restrictive. And in practice there is no clue how to test this assumption. Is this assumption necessary?\n\nBesides Assumptions A5(a), A5(b), A5(c), why not consider the situation that \\alpha(X) is known but \\beta(X) is unknown.\n\nSince Assumption A5 is already unrealistic and restrictive, I feel the differences among the assumptions A5(a), A5(b), A5(c) are only for some sort of theoretical understandings—they do not provide any meaningful guidance for applications.\n\nThe whole section 4.2 follows the standard procedure of deriving the semiparametric efficiency bound in the literature. However, it is not presented clearly. Both CATE and ATE are quantities of interest, what you presented are for CATE, or for ATE? What is the other one?\n\nIn Section 4.3, only quantifying the misspecification bias is not good enough. Is there is a way to debias it?\n\nIn Section 4.4, it is not convincing: why there will be finite-sample gain but this gain will diminish when the sample size goes to infinity? Does that make sense?\n\nHave the authors considered the situation that S=1 has a lot more samples than S=0. What would the story be in that situation?\n\nOne real data example is not sufficient. The authors should use a couple of benchmark datasets to demonstrate the method they study in this paper.", "limitations": "No the authors did not address the limitations or potential negative societal impact of this work.", "rating": 1, "confidence": 4, "soundness": null, "presentation": null, "contribution": null, "strengths": "", "weaknesses": "", "quality": 2, "clarity": 1, "significance": 1, "originality": 1, "strengths_and_weaknesses": "Strengths:\nThis is an interesting setting, especially in the causal inference community, considered for data integration in order to achieve some sort of benefits.\n\nWeaknesses:\nThe conclusions are not clear to me; see my specific questions below. Further, it is unclear why we want to consider the data integration problem in such a setting.\nSome of the theoretical results are problematic; see my specific questions below.\nOnly one real data experiment is not sufficient; multiple experiments on benchmark data are needed.", "was_revised": true, "final_justification": "The authors slightly partially solved my concerns; however, a few major fatal issues remain. It is hard to convince myself to increase the rating for this work.\n\nThe overall goal of paper is unclear, or, at least, unclearly articulated. If the goal is to just provide a cautionary note, please make sure this note itself is worthwhile and convincing. For the estimator the authors newly propose, the writing is unclear or even incorrect in a few aspects, e.g., the question in my last comment.\n\n> The relationship between ATE and CATE efficiency is direct: since ATE = E[CATE], any efficiency bound for ATE provides an upper bound for CATE estimation efficiency.\n\n> This cannot be true. Expectation is average. Why every bound for ATE provides an UPPER bound? More importantly, if CATE is generally a function of X, how can its efficiency bound be defined?\n\nFinally, with respect to the real data analysis, the authors declined to include additional analyses due to a lack of available datasets with disparate outcome measures. Yet they also assert that in fields like public health, social sciences, and healthcare, such data are common. This contradiction undermines the rationale provided. If these datasets are indeed prevalent, where are they? The logic here seems inconsistent.", "rebuttal": "We sincerely thank the reviewer for their detailed and thoughtful feedback. We appreciate the opportunity to improve our manuscript. Below, we address the main concerns raised.\n\n---\n\n### 1. Purpose and Central Contribution\n\nThank you so much for your thoughtful question. We would like to emphasize that the central focus of our paper is **not the proposal of a new estimator**, but rather a general cautionary message about the challenges and limitations of data integration in the presence of disparate outcome measures.\n\nIn fields such as public health, social sciences, and healthcare—where high-quality, causally informative data are often limited—data integration has emerged as a promising strategy to improve precision and support evidence-based decision-making. However, due to variations in study design, implementation logistics, and measurement protocols, different studies frequently assess the same underlying construct using different outcome measures.\n\nTo the best of our knowledge, the existing causal inference literature does not offer principled guidance on when such data integration is beneficial, or even valid. Our paper is among the first to formally characterize the conditions under which integrating data with disparate outcomes can lead to efficiency gains—and when it cannot.\n\nOur theoretical results show that:\n\n* **Asymptotic efficiency gains** are only achievable under strong, often untestable assumptions about the relationship between outcomes across datasets;\n* **Finite-sample gains** may be possible under milder assumptions, but we precisely quantify when and to what extent. These gains are often modest and tend to vanish as sample size increases;\n* There is a **significant risk of bias** if the required assumptions are violated, making the integration not just unhelpful but potentially misleading.\n\nTo illustrate these findings, we include a real data case study that mirrors and reinforces our theoretical conclusions. We have updated the introduction to better emphasize this central message and added the following summary statement:\n\n> *“This paper provides a cautionary framework for data integration in the presence of disparate outcomes, demonstrating that while such integration may offer marginal gains under ideal conditions, it carries a high risk of bias when assumptions are violated. To the best of our knowledge, we offer the first formal quantification of this tradeoff and emphasize the need for careful scrutiny before applying such methods in practice.”*\n\n---\n\n### 2. Assumption Clarifications and Structural Model Updates\n\n**Error Distribution:**\nThank you so much for pointing this out. You are correct—we do **not** require the errors to follow a normal distribution. Our results only rely on the assumption that the errors have finite variance. We have updated the structural model descriptions and clarified the corresponding assumptions in the theoretical results to reflect this more precisely. Importantly, this correction has no impact on the conclusions of the paper, as none of our derivations or results depend on normality.\n\n**Partial Linearity and Assumption Strength:**\nThank you for highlighting this important point.\nFirst, we want to clarify that our results are derived under a partial linear relationship between $Y$ and $W$: while the dependence between $Y$ and $W$ may be nonlinear, it is moderated through $X$. This structure is chosen for parsimony, to make our argument as transparent and interpretable as possible.\n\nThe central point we aim to make is that even under this strong structural assumption, efficiency gains from incorporating auxiliary data are not guaranteed, unless the dependency between outcomes is almost fully known. By demonstrating the lack of gain under the partial linear assumption (A.5), we are making a stronger statement: that if efficiency gains are not possible even in this idealized setting, they are even less likely under more general, nonlinear relationships.\n\n**On Untestable Assumptions:**\nSecond, all causal inference relies on untestable assumptions. This is also true about data integration for the causal inference literature. If we do not have data of both $Y$ and $W$ measured for the same individuals, then we need to rely on untestable assumptions. The key point of this paper is that such untestable assumptions are very common in the literature, but there is hardly any scrutiny on the cost vs benefit. Our work is one of the first to try it, principally for the scenario described in the paper.\n\n**Generalizing the Model Structure:**\nThird, in response to your suggestion, we have extended our analysis by relaxing the linearity assumption. Specifically, we consider a more general setting in which:\n\n$$\nY = \\alpha(X) \\cdot \\zeta(W) + \\beta(X) + \\text{noise}\n$$\n\nwhere $\\zeta$ is an arbitrary (possibly nonlinear) function of $W$. We find that even in this more flexible setup, efficiency gains are only achievable when both $\\alpha(X)$ and $\\zeta(W)$ are known, mirroring our original findings. This reinforces our core message: without strong, often untestable assumptions about the functional relationship between disparate outcomes, integrating auxiliary data does not yield reliable efficiency gains.\n\n**Bias Cannot Be Removed Without New Untestable Assumptions:**\nUnfortunately, there is no way to *debias* the bias due to misspecification of $\\alpha$ without making additional untestable assumptions. This is indeed the key point of our paper—that there is no free lunch.\n\n---\n\n### 3. Finite-Sample Gains and the Role of Auxiliary Sample Size\n\nThank you for the opportunity to clarify this point further. A central motivation for our work is the setting where the **auxiliary dataset is much larger** than the primary dataset, common in public health, social science, and healthcare applications.\n\nWe have expanded the discussion following **Theorem 6** to articulate when and why **finite-sample efficiency gains** may arise in such settings. \n\nTo explore this in depth, our simulation study (presented in the Appendix) systematically examines how results vary with the **ratio of sample sizes** ($n_1/n_0$), the **dimensionality of covariates**, and the **overall sample size**. These empirical results reinforce the theoretical insights described above.\n\nWe have added the following clarifications to the discussion of Theorem 6:\n\n> *“Finite-sample efficiency gains from incorporating auxiliary data arise when the function $\\alpha(X)$, capturing the dependence between $Y$ and $W$, is simpler to estimate than $\\mu_Y(X)$. In such cases, one may first estimate $\\mu_W(X)$ using auxiliary data, and then use the combined data to estimate $\\alpha(X)$. However, the existence and extent of these gains depend on the relative complexity of the function classes and the sample sizes involved. As $n_0$ increases, the benefit of this two-stage strategy diminishes, and asymptotically, both the direct and the auxiliary-based estimators converge to the same efficiency.”*\n\n> *“The first term captures the gain from replacing the full function class $M_Y$ with a lower-complexity class $\\mathcal{A}$, and the second term reflects the accuracy of estimating $\\mu_W(X)$ from the auxiliary data. Gains are most pronounced when $\\omega_\\alpha \\ll \\omega$ (i.e., when $\\alpha(X)$ is much simpler than $\\mu_Y(X)$) and when $n_1 \\gg n_0$ (i.e., when we have a large auxiliary dataset relative to the primary dataset). This characterization formally supports the intuition that structural assumptions, when coupled with abundant auxiliary data, can yield meaningful finite-sample gains—even though such gains vanish asymptotically.”*\n\n---\n\n### 4. Real Data Case Study\n\nRegarding the suggestion to include an additional real data benchmark case study, we respectfully disagree with the reviewer's interpretation. This paper does not propose a new method, and the goal of the case study is not to demonstrate the effectiveness of any particular estimator. Rather, the case study serves a different and important purpose: it illustrates how both point estimates and uncertainty quantification evolve as progressively stronger assumptions are imposed, highlighting the inherent tradeoff between precision and validity in data integration with disparate outcomes.\n\nThe central message of the case study—and the paper as a whole—is that **there is no free lunch** in data integration. Gains in efficiency may come at the cost of relying on strong, untestable assumptions, which can, in turn, introduce bias. This example underscores the broader cautionary tale of our work: data integration can be tempting, but without critical evaluation of underlying assumptions, it may lead to misleading conclusions.\n\nFurthermore, we wish to emphasize that, unlike in machine learning or deep learning, *data integration in causal inference with disparate outcomes lacks benchmark datasets with known ground truths*. This fundamental difference limits the applicability of empirical validation strategies commonly used in other disciplines. In causal research, the evaluation of assumptions—and understanding the consequences of their violations—is often the most principled way to assess a method’s utility.\n\n---\n\n### 6. Noise Variance\n\nThanks for this nuanced question. For the sake of the parsimony of the theory section, we assume $\\sigma_Y$ and $\\sigma_W$ are known. However, one can consistently estimate the variance of noise terms in $Y$ and $W$ (under the homoskedasticity assumption) by calculating the variance of $Y - \\hat{Y}$ and $W - \\hat{W}$. Regarding the efficiency bound, this will add two terms regarding the uncertainty due to the estimation of $\\sigma_Y$ and $\\sigma_W$. However, note that **our no-free-lunch conclusion does not change**.\n\n---\nWe hope this thorough response addresses your concerns and clarifies the broader motivation and contribution of our paper. We sincerely appreciate the opportunity to improve the clarity and rigor of our work."}, {"review_id": "eizGD6qwGa", "reviewer": "Reviewer_261G", "summary": "This paper investigates the integration of studies with different outcome measures for causal inference. It shows that combining such datasets can improve estimation efficiency only under strong assumptions about how the outcomes are related. Weaker assumptions may yield finite-sample benefits, but these gains vanish asymptotically and carry a risk of bias if misspecified. The framework is demonstrated using opioid treatment studies with differing withdrawal scales (SOWS vs. COWS).\n\nDue to the high amount of papers I am forced to provide only a short high level review.", "questions": "-", "limitations": "-", "rating": 5, "confidence": 2, "soundness": null, "presentation": null, "contribution": null, "strengths": "", "weaknesses": "", "quality": 3, "clarity": 3, "significance": 3, "originality": 2, "strengths_and_weaknesses": "Strengths:\n\n- the paper is well executed and also grounded in practical examples\n- the problem is relevant, it belongs to a niche within the rather broad conference\n- the writing is clear and easy to follow\n- I particularly like section 5\n\nWeaknesses:\n- the theoretic exposition in Section 4 is rather simple. I do not see any surprising or particularly interesting results.\n- I would have appreciated it if the authors put more focus on the experimental study, which I think is the more important aspect of this paper", "was_revised": true, "final_justification": "I read the author rebuttal and thank them for the explanation. I raised the score to an accept.", "rebuttal": "* Thank you very much for your constructive comments -- we appreciate it. Following your suggestion, we have revised the introduction to place greater emphasis on our real data case study. Specifically, we now use the case study to motivate our central question: When can data integration with disparate outcomes yield benefits? We also preview our empirical findings in the introduction, highlighting the fundamental tradeoff between gains in precision and the strength of assumptions required to achieve them.\n> “In our case study, we assess whether XT-NTX is more effective than BUP-NX in reducing withdrawal symptom severity. The point estimate from the primary study is slightly negative, suggesting a marginal advantage for XT-NTX, but the 95% confidence interval includes zero—indicating no statistically significant difference between the two treatments (see Figure 1(b); estimate $\\hat{\\theta}_0$). To improve estimation precision, we explore leveraging auxiliary data. Under the strong assumption our combined analysis yields a statistically significant result favoring BUP-NX over XT-NTX (see Figure 1(b); estimate $\\hat{\\theta}_a$).. While such findings may appear actionable, they hinge critically on an untestable assumption linking outcomes Y and W. If this assumption is violated, the resulting estimates may be misleadingly precise. Our case study thus serves as a cautionary example: although integrating auxiliary data can improve precision, it must be done with careful scrutiny of the underlying assumptions, which—if invalid—can lead to confidently incorrect conclusions.\"\n* Regarding the theoretical results: \nData integration is gaining significant traction in causal inference and machine learning, particularly for enhancing statistical efficiency in applications across public health, public policy, and healthcare. In practice, disparate outcomes across datasets are quite common—often arising due to differences in study design, logistics, or measurement protocols. While practitioners routinely rely on heuristics to integrate such datasets, to the best of our knowledge, the literature lacks formal investigation into when and under what conditions such integration leads to real benefits. Our paper addresses this gap with a set of novel theoretical results that:\n> 1. Quantify the conditions under which asymptotic efficiency gains are possible, and measure their magnitude;\n> 2. Characterize the finite-sample benefits and limitations—an aspect that is rarely studied, yet highly relevant for practical applications;\n> 3. Identify and quantify the risks of integrating datasets with non-equivalent outcome measures, especially under violated assumptions.\n\nWe are confident these results provide a principled foundation for our overarching cautionary message: while data integration holds promise, its success depends critically on strong and often untestable assumptions. Our work offers both a theoretical framework and empirical motivation to guide responsible and assumption-aware integration of datasets with disparate outcomes."}]

Author rebuttal:

Meta-review: My recommendation is to accept the paper. This decision was close because there was strong disagreement among reviewers. I hope that the authors will take all feedback into account when making revisions for the camera-ready.

Three reviewers found the message to be a valuable contribution, warning against a plausible pitfall in data integration. There were some issues raised by these reviewers, but overall they supported the message, the analysis, and the example given in the main text.

One reviewer found the paper under-motivated. To address this concern, I think it would be useful for the authors to include reference(s) to at least one study that attempts this data integration in the current literature (perhaps as part of a meta-analysis?). This would motivate the need for a cautionary note against current or emerging practice.

It would also be useful to clarify the scope of the theory. In specific, being very clear that the theoretical claims are about ATE estimation, and not CATE estimation would be useful. More broadly, explicitly stating the scope of the conclusions from the theory (i.e., that if things don't work in the restrictive linear context, we would expect them to fail in more complex contexts) would be useful.

Better integrating the simulated demonstrations of the theory into the main text, as some reviewers requested, would also be useful.
Decision: Accept (poster)