# Cross-Institutional Transfer Learning for Educational Models:
Implications for Model Performance, Fairness, and Equity

Josh Gardner<EMAIL_ADDRESS>0000-0002-4998-5918 University of
Washington ,  Renzhe Yu<EMAIL_ADDRESS>0000-0002-2375-3537 Teachers
College & Data Science Institute, Columbia University ,  Quan Nguyen
<EMAIL_ADDRESS>0000-0001-8937-5121 University of British Columbia ,
Christopher Brooks<EMAIL_ADDRESS>0000-0003-0875-0204 School of
Information, University of Michigan and  Rene F. Kizilcec
<EMAIL_ADDRESS>0000-0001-6283-5546 Department of Information Science,
Cornell University

(2023)

###### Abstract.

Modern machine learning increasingly supports paradigms that are multi-
institutional (using data from multiple institutions during training) or
cross-institutional (using models from multiple institutions for inference),
but the empirical effects of these paradigms are not well understood. This
study investigates cross-institutional learning via an empirical case study in
higher education. We propose a framework and metrics for assessing the utility
and fairness of student dropout prediction models that are transferred across
institutions. We examine the feasibility of cross-institutional transfer under
real-world data- and model-sharing constraints, quantifying model biases for
intersectional student identities, characterizing potential disparate impact
due to these biases, and investigating the impact of various cross-
institutional ensembling approaches on fairness and overall model performance.
We perform this analysis on data representing over 200,000 enrolled students
annually from four universities without sharing training data between
institutions.

We find that a simple zero-shot cross-institutional transfer procedure can
achieve similar performance to locally-trained models for all institutions in
our study, without sacrificing model fairness. We also find that stacked
ensembling provides no additional benefits to overall performance or fairness
compared to either a local model or the zero-shot transfer procedure we
tested. We find no evidence of a fairness-accuracy tradeoff across dozens of
models and transfer schemes evaluated. Our auditing procedure also highlights
the importance of intersectional fairness analysis, revealing performance
disparities at the intersection of sensitive identity groups that are
concealed under one-dimensional analysis.111Code to reproduce our experiments
is available at https://github.com/educational-technology-collective/cross-
institutional-transfer-learning-facct-2023.222© Gardner et al.2023. This is
the author’s version of the work. It is posted here for your personal use. Not
for redistribution. The definitive version was published in ACM FAccT 2023,
https://doi.org/10.1145/3593013.3594107

Algorithmic Fairness, Education, Dropout Prediction, Transfer Learning,
Intersectionality

††journalyear: 2023††copyright: acmlicensed††conference: 2023 ACM Conference
on Fairness, Accountability, and Transparency; June 12–15, 2023; Chicago, IL,
USA††booktitle: 2023 ACM Conference on Fairness, Accountability, and
Transparency (FAccT ’23), June 12–15, 2023, Chicago, IL, USA††price:
15.00††doi: 10.1145/3593013.3594107††isbn: 979-8-4007-0192-4/23/06††ccs:
Applied computing Law, social and behavioral sciences††ccs: Applied computing
Education††ccs: Computing methodologies Machine learning

##  1\. Introduction

Improvements in digital infrastructure have enabled numerous applications of
machine learning across domains but in decentralized organizational contexts
(e.g., universities, schools, hospitals, finance, and government), the
capacity to use machine learning typically depends on the availability of
local infrastructure and resources. Under-resourced institutions may therefore
be unable to reap the full benefits of machine learning applications despite
commonly having the greatest need. Externally developed models have
increasingly been adopted in these cases to address this challenge. While this
highlights a potential benefit of sharing predictive models within large-scale
cross-institutional collaborations, the risks and benefits of cross-
institutional modeling are not well understood, particularly in terms of the
potential impact on the most vulnerable populations affected by these models.

Figure 1. Summary of cross-institutional transfer methods evaluated in this
work (transfer methods defined in Section 4.3). Each point represents one
cross-institutional transfer trial (see Section 6) with an $L_{2}$-regularized
logistic regression model. (See Figure 7 for results with LightGBM, MLP
models.)

We investigate the benefits and risks of cross-institutional transfer in the
context of an important and pervasive application of machine learning in
education: university student dropout prediction. Every year, over one million
students drop out of college in the United States, and they are 100 times more
likely to default on their student loan payments than those who graduate
(Kantrowitz, 2021). This leaves young adults with a major financial burden and
little to improve their job prospects with an incomplete degree (Schneider and
Yin, 2011). Dropout rates are especially high for students from minority
groups333https://nces.ed.gov/programs/raceindicators/indicator_red.asp,
exacerbating existing inequities.

Lowering college dropout rates is a priority for many institutions of higher
education. U.S. federal regulations incentivize colleges and universities to
reduce dropout by requiring them to report dropout rates, performance-based
funding (Hillman et al., 2014), and college rankings that account for
graduation rates (Alsmadi et al., 2020). This has led an increasing number of
colleges and universities to adopt data-driven predictive models to identify
at-risk students, in order to intervene early enough to support students
before they drop out. While private vendors such as Civitas, Starfish
Retention, and Hobsons sell software for at-risk prediction to institutions,
they do not share the technical details of underlying models. This limits the
ability of practitioners and researchers to audit the performance and possible
biases of these models’ predictions, especially for institutions other than
those where models were trained (Kizilcec and Lee, 2022; Baker and Hawn,
2021).

Concerns about algorithmic bias in education have motivated several recent
studies that interrogate the fairness and ethics of predictive modeling in
education (Gardner et al., 2019; Kizilcec and Lee, 2022; Lee and Kizilcec,
2020; Yu et al., 2021, 2020). Inter-university data partnerships, such as the
Unizin Consortium444https://unizin.org/, have also emerged to standardize data
infrastructure, provide opportunities for multi-institutional model
development by using data from multiple institutions during training, and even
facilitate cross-institutional model sharing. However, the benefits and risks
of this form of transfer learning are presently understudied, and studying
cross-institutional learning in a research context can be challenging due to
data privacy regulations: in most circumstances, student data cannot simply be
shared between institutions or uploaded into public repositories due to
federal regulations.

In this work, we seek to evaluate the implications for model performance and
fairness of three approaches to cross-institutional transfer learning. We
conduct the first large-scale, systematic analysis of cross-institutional
transfer learning in higher education. We evaluate three transfer approaches
(Section 4.3) motivated by real-world data, collaboration models, and
institutional needs in higher education. We use datasets from four U.S.
universities with diverse student populations (Section 4.1), propose metrics
to evaluate model performance and fairness in cross-institutional transfer
learning (Section 4.4), conduct a comprehensive set of experiments to measure
the effects of different transfer approaches on the proposed metrics in terms
of (a) overall performance (Section 6.1) and (b) fairness measured by
intersectional performance disparities (Section 6.2), and evaluate fairness-
performance tradeoffs (Section 6.3). Our main results are summarized in Figure
1. We discuss limitations and recommendations for future work in Section 7.

Our contributions: While prior research has explored prediction models based
on multi-institutional educational datasets, to our knowledge, our work is the
first to systematically investigate the implications of cross-institutional
transfer learning for fairness and equity. This work required a year-long
effort working with each institution to develop a common data schema to map
their local data into this schema to enable cross-institutional learning. We
contribute a novel methodology for auditing cross-institutional transfer
learning, including metrics for measuring intersectional fairness of model
transfer. Finally, our empirical results provide a useful benchmark for
researchers and practitioners interested in cross-institutional transfer
learning both within and outside of the domain of education. Our results
demonstrate that (i) cross-institutional transfer is feasible even when no
historical training data is present at a target institution (e.g., via direct
or voting transfer); (ii) a simple zero-shot voting transfer method achieves
similar performance to a local model for all institutions in our study,
without requiring any local training data and at no cost to fairness; (iii)
stacked ensembling provides no additional benefit over local training or zero-
shot voting transfer from other institutions; and (iv) there does not exist a
strict empirical tradeoff between fairness and accuracy across our broad set
of models, transfer schemes, and institutions evaluated.

##  2\. Related Work

###  2.1. College Dropout Prediction

Higher education institutional data are increasingly used for research and
applications to predict and explain factors contributing to student dropout
(Tinto, 1975; Kuh et al., 2007). These models and applications, often in the
form of early warning systems, can help identify which students might be
struggling and at what time in their academic journey. This information can be
used to provide proactive, targeted support or interventions. Several previous
studies have investigated the task of dropout prediction in higher education
(Aulck et al., 2019; Dekker et al., 2009; Jayaprakash et al., 2014; Del
Bonifro et al., 2020; Beaulac and Rosenthal, 2019; Berens et al., 2019; Hutt
et al., 2019; Yu et al., 2021; Bird et al., 2021; Luo and Pardos, 2018; Chen
et al., 2018; Ameri et al., 2016). These studies are conducted across
different institutional contexts, but the core learning problem they address
is framed as a binary classification task, where structured features about
students’ educational history, demographics, or academic records in the early
phase of college are extracted from administrative data to predict
dropout/persistence at a later stage. Learned models are evaluated using
binary classification metrics and state-of-the-art models using students’ pre-
college characteristics and early college records can predict whether a
student will drop out within the first year with an AUC-ROC between 0.7 and
0.9 across various countries and institutions (Berens et al., 2019; Bird et
al., 2021; Ameri et al., 2016; Chen et al., 2018). These promising results
have continued to motivate research into dropout prediction modeling to aid
student support services and institutional policy-making. However, there has
been little research that empirically examines cross-institutional dropout
prediction.

###  2.2. Disparate Impacts and Fairness- Performance Tradeoffs in Machine
Learning

A great deal of prior work has explored both empirical and algorithmic
approaches to “fairness” in machine learning, which is often concerned with
how an objective function or conditional risk estimate varies across subgroups
(Corbett-Davies and Goel, 2018). The current study is most closely related to
previous works that explore the disparate impact of machine learning methods,
and the interaction between fairness and predictive performance in machine
learning.

Recent work finds that different learning techniques and contexts can result
in a disproportionate impact on subgroups, even when these techniques are not
explicitly targeted toward subgroups in any way, and even when they improve
some average measure(s) of performance. Disproportionate impacts have been
demonstrated in the use of differential privacy (Bagdasaryan et al., 2019),
model compression (Hooker et al., 2020), model simplification (Kleinberg and
Mullainathan, 2019), selective classification (Jones et al., 2020), synthetic
data generation (Cheng et al., 2021), under the presence of feature noise
(Khani and Liang, 2020), and in repeated (i.e. multi-round) loss minimization
(Hashimoto et al., 2018).

There have been some formal analysis of potential tradeoffs between fairness
and various measures of model performance (Cummings et al., 2019; Feldman et
al., 2015; Yu et al., 2021), but our theoretical understanding remains limited
in many areas. Empirically, however, there is some evidence that there are
_no_ strict tradeoffs between model performance and fairness under certain
conditions. For example, Rodolfa et al. (2021) finds that fairness-enhancing
interventions across policy programs in education, mental health, criminal
justice, and housing safety improved fairness with negligible effects on model
accuracy. In education, a recent study found no evidence of a strict tradeoff
between model performance and fairness predicting dropout from massive open
online courses Gardner et al. (2019). However, the degree to which these
findings apply to university student dropout or retention models is unknown.

Research on algorithmic fairness in education has mostly investigated whether
supervised learning models trained on the entire student population generate
systematically biased predictions of individual outcomes such as correct
answers(Doroudi and Brunskill, 2019), course grades (Yu et al., 2020),
university (Yu et al., 2021) and MOOC dropout (Gardner et al., 2019), learned
representations of student writing (Arthurs and Alvero, 2020; Loukina et al.,
2019), and graduation (Hutt et al., 2019; Kung and Yu, 2020); it has also
explored algorithms for at-risk prediction under fairness constraints (Hu and
Rangwala, 2020). Overall, this area of research is nascent and in need of
systematic frameworks specific to educational contexts to map an agenda for
future research. It does suggest, however, that analyses of novel learning
paradigms (such as cross-institutional transfer) should include thorough
auditing for fairness, a goal of the current study.

###  2.3. Cross-Institutional Learning

We introduce the term cross-institutional learning to describe the context
where data is partitioned across a set of institutions by observation (i.e.,
each institution has a set of records with the same features, but collectively
training on all institutions’ centralized data is not possible). Prior work
related to cross-institutional modeling has used a variety of different
monikers, including “cross-silo” (Kairouz et al., 2019), “horizontal” (Yang et
al., 2019), “collaborative” (Sheller et al., 2020), and transfer learning.

Recent advances in both tooling and theory have, in principle, enabled
improved access to cross-institutional training. In the past five years,
several usable open-source frameworks for distributed, decentralized machine
learning555e.g. TensorFlow Federated https://www.tensorflow.org/federated, IBM
Federated Learning https://ibmfl.mybluemix.net/ as well as frameworks for
privacy-preserving learning666TensorFlow Privacy
https://github.com/tensorflow/privacy, Opacus https://opacus.ai/ have emerged.
Theoretical advances, such as various approaches to differentially-private
model training (DP-SGD (Abadi et al., 2016), PATE (Papernot et al., 2018))
have provided provable guarantees regarding non-identifiability of model
training examples, which may reduce privacy concerns related to cross-
institutional collaboration and further pave the way for cross-institutional
training in practice. The development and refinement of techniques such as
federated learning and secure multi-party computation or homomorphic
encryption has also enabled distributed training with improved privacy and
security (Kairouz et al., 2019).

Prior work has also investigated the related theoretical problem of learning
fair models when the test distribution differs from the training distribution,
as may be the case in cross-institutional learning. For example, Cotter et al.
(2019) studies the use of constrained optimization to improve the satisfaction
of a fairness constraint on a held-out dataset with a possibly different
distribution from the training set, Coston et al. (2019) evaluates mitigating
unfairness on a target domain due to covariate shift when sensitive attributes
are unknown, and Singh et al. (2021) explicitly investigates fairness under
distribution shift. Algorithms which are “fairness-preserving” have been shown
to be sensitive to variations in random train-test splits (Friedler et al.,
2019), suggesting that the fairness properties of models developed using such
algorithms are brittle across distributions.

Applied research on cross-institutional learning has been somewhat limited. In
the medical domain, cross-institutional learning has been used for brain tumor
segmentation (Sheller et al., 2018; Sheller et al., 2020), diabetic
retinopathy diagnosis, and mammography screening (Chang et al., 2018). For
example, in the context of a tumor segmentation model, direct transfer leads
to average performance degradation at varying levels for 9 of 10 institutions
evaluated, while collaborative learning improves performance and performs
similarly to data-sharing, depending on the approach used (Sheller et al.,
2020) and can be similar to the performance of centralized models in simulated
settings (Matschinske et al., 2021). Chang et al. (2018) evaluates several
transfer scenarios (local, ensembling via prediction averaging, single weight
transfer, cyclical weight transfer) and finds that ensembling and weight
transfer both outperformed local models in terms of validation and testing
accuracy. Pessach et al. (2021) looks into the task of collaboratively
training fair models across institutions through a preprocessing mechanism
which leads to fairness improvement. However, the impact of the intervention
on individual institutions’ models and institutional subpopulations is
unclear.

In the domain of education, there have been some research efforts that
formulate and empirically examine the issue of model transferability across
instructional, institutional, and even societal contexts (Jayaprakash et al.,
2014; Ocumpaugh et al., 2014; Li et al., 2021; Ding et al., 2019; Lagus et
al., 2018; Boyer and Veeramachaneni, 2015). For example, Ocumpaugh et al.
(2014) found that models detecting students’ affective states in tutoring
systems do not transfer well when trained on one student population and tested
on another, especially when rural students are the target (test) population.
Similarly, Li et al. (2021) investigated whether academic achievement
prediction models trained on U.S. samples can generalize to other national
contexts, and found that the performance drops significantly for less
developed countries. Most closely related to the current study, Jayaprakash et
al. (2014) trained an early alert system of academically at-risk students at a
liberal arts college and applied the model to four partner institutions with
different institutional profiles. They found that the predictive performance
declined but was still practically useful – the recall of at-risk students
only dropped from 85% at the source institution to between 61% to 84% (an
average of 75%) at the target institutions. These efforts show the promise of
cross-institutional educational models especially when low-resourced
institutions cannot afford to develop their own model, but still require more
research to ensure that performance does not degrade across institutions,
harming vulnerable students.

##  3\. Present Study and Research Questions

Under the Family Educational Rights and Privacy Act (FERPA), U.S. higher
education institutions are required to maintain records about students and
enrollments for purposes of external reporting (e.g., to federal educational
authorities) and internal improvement. Local student information systems (SIS)
are widely used to manage these records and can facilitate the identification
of students who are at risk of failing classes, not graduating on time, or
dropping out (see Section 2.1). Due to shared reporting responsibilities,
common operational routines, and similar software tools, institutions tend to
have many overlapping features in their SIS data (e.g., students’ course
enrollments and demographic characteristics).

Our study leverages this commonality across four universities in order to
explore the impacts of cross-institutional educational modeling. As discussed
in Section 2.3 above, the limited prior work on cross-institutional transfer
learning has suggested that direct transfer of learned models across
institutions tends to degrade performance, and that only specialized weight-
sharing strategies allow institutions to realize performance gains from
transfer learning. In addition, little research has evaluated the fairness
implications for such transfer scenarios. Building on these previous insights,
our research addresses the following three research questions within the
domain of dropout modeling in higher education:

RQ1. How does cross-institutional transfer (direct, voting, and stacked)
affect performance relative to a local model?

RQ2. How does cross-institutional transfer affect the (intersectional)
fairness of the resulting model?

RQ3. Is there a tradeoff between model performance and fairness under cross-
institutional transfer?

##  4\. Methods

###  4.1. Data and Preprocessing

We use (de-identified) data from four public universities in the United
States. All data is for first-time, first-year students in four-year
bachelor’s programs. Our dataset represents a wide range of enrollment sizes,
demographic compositions, and first-year retention rates as summarized in
Table 1.

Institution |  Ntrain |  Female |  URM |  Hispanic |  Asian |  Black |  Native Amer. |  Two or more |  White |  First-year Retention
---|---|---|---|---|---|---|---|---|---|---
A |  20k |  49% |  40% |  26.7% |  7.1% |  5.1% |  1.5% |  5.1% |  53.3% |  80%
B |  1k |  63% |  24% |  12.6% |  2.9% |  5.7% |  0.9% |  4.3% |  72.8% |  57%
C |  20k |  57% |  36% |  33.1% |  47.9% |  3.2% |  0.0% |  0.0% |  12.9% |  94%
D |  30k |  55% |  14% |  6% |  11.9% |  5.3% |  0.0% |  4% |  67.5% |  98%
Table 1. Summary statistics for the training dataset for each institution
showing demographic characteristics according to federal reporting
requirements (URM: underrepresented racial minority; Two or more: multiple
racial/ethnic groups).

We study the effects of cross-institutional transfer by converting the raw
student information system (SIS) data obtained from each institution into a
shared schema. Due to restrictions on data sharing, each institution’s data
was preprocessed separately and then validated by a shared pipeline prior to
modeling. Only the learned model weights, not the data nor any intermediate
artifacts (such as gradients during training), were shared outside of each
institution. A goal of this project is to use SIS data in a form as close to
its raw format as possible (i.e. minimal additional feature engineering),
while also retaining the maximum number of viable features for experiments. In
practice, this required balancing (i) removing features when insufficient data
was available for all institutions or operationalization of variables was
irreconcilable, and (ii) identifying ways to map related but non-identical
features at each institution into a common semantic space. The process of
defining a shared schema and processing the raw exports of each institution’s
SIS required domain expertise as well as familiarity with each institutional
dataset.

The full schema produced by all institutions for our analysis is described in
Table 2. Each row in the dataset represents a student enrolled in the fall
term. The features describe students’ academic history, demographics, current
course load and course topics, and future plans (e.g., majors and minors).
While the classification of gender as binary and the specific ethnic and
racial groups raises concerns, we rely on the student categories used by the
institutions themselves, which are shaped by federal reporting requirements.
We provide further details on the schema in Section B.1. We release our code
to validate cross-institutional datasets for conformity to this schema, and to
replicate experiments using these features.777https://github.com/educational-
technology-collective/cross-institutional-transfer-learning-facct-2023

###  4.2. Task

Our target prediction is first-year retention: for each student who enters an
institution for the first time in the fall, we predict a binary indicator for
whether that student will enroll at the same institution the following fall.
This target matches the National Student Clearinghouse’s definition
888https://nscresearchcenter.org/persistence-retention/, and is widely used
both in research (Section 2.1) and practice in education.

We embrace the data constraints faced by educational institutions, which can
limit the applicability of some previously proposed techniques for transfer
learning. Federal regulation to protect student data privacy (FERPA) creates
challenges for data sharing: costs associated with determining whether data
may be shared, and then facilitating the sharing may be intractable for many
institutions. We, therefore, do not consider techniques, such as federated
learning, which require collaborative training in any form. For similar
reasons, we do not consider approaches that require data sharing, for example,
for training a centralized model on a joint dataset. Instead, we evaluate the
realistic setting where each institution can only share model weights and only
a single round of cross-institutional weight sharing is possible. In our
experiments, the barriers between institutional datasets are real, as are the
challenges of cross-institutional transfer. Contrast this with prior work on
cross-institutional transfer or fairness under domain shift discussed in
Section 2.3, which frequently simulated different “institutions” or “domains”
by synthetically partitioning a single dataset.

###  4.3. Three Approaches to Cross-Institutional Transfer

Institutions in almost every domain, and particularly in higher education,
differ in (i) data capacity, and (ii) modeling capacity. As a result,
institutions vary in how they may be able to develop or utilize cross-
institutional models. We define three distinct approaches to cross-
institutional transfer, intending to cover three common contexts where
institutions may seek to utilize cross-institutional models. We term these
direct transfer, voting transfer, and stacked transfer. As a baseline for
comparison, we consider a local model trained at the same institution where it
is tested.

We consider a dataset $\mathcal{D}_{k}\coloneqq
X_{k},Y_{k}=(x_{i},y_{i})_{i=1}^{n}\sim\mathcal{P}_{k}$ of i.i.d. observations
drawn from distribution $\mathcal{P}_{k}$, where $|x_{i}|=d$ features are
present and $k$ represents an institution of interest. Denote
$f(\theta,\cdot)$ as a model with parameters $\theta$, where
$f(\theta,x_{j})=\mathbb{P}(y_{j}=1|x_{j})$ is the model’s predicted
probability that $x_{j}$ has label 1, noting that $j$ indicates a potentially
different institution of interest, and thus $x_{j}$ may come from a
distribution $\mathcal{P}_{j}$ which is different from $\mathcal{P}_{k}$.
Denote the parameters estimated by training $f$ on $\mathcal{D}_{k}$ as
$\hat{\theta}(\mathcal{D}_{k})$. Denote the loss (for some general loss
function) of a model trained on distribution $k$ and evaluated on distribution
$\ell$ as
$\mathcal{L}\Big{(}f(\hat{\theta}(\mathcal{D}_{k}),\tilde{X}_{\ell}),\tilde{Y}_{\ell}\Big{)}$,
where $\tilde{\mathcal{D}_{k}}\coloneqq\tilde{X}_{k},\tilde{Y}_{k}$ indicates
the test split from a distribution $k$. We use $\mathcal{I}$ to refer to the
set of all institutions.

We define each of the transfer learning approaches used in our experiments as
follows:

Local: A local model is one trained on the same institution from which it is
evaluated. That is, for institution $k$, the performance of a local model is
defined by
$\mathcal{L}\Big{(}f(\hat{\theta}(\mathcal{D}_{k}),\tilde{X}_{k}),\tilde{Y}_{k}\Big{)}$.

Direct Transfer: A direct transfer scenario is one where a model is to be
deployed to an institution different from its testing institution. That is,
for institutions $k$, $j$, the direct transfer model performance is measured
by
$\mathcal{L}\Big{(}f(\hat{\theta}(\mathcal{D}_{k}),\tilde{X}_{j}),\tilde{Y}_{j}\Big{)}$.
We refer to $k$ as the source institution and $j$ as the target institution,
following the domain transfer literature. A single trained source model can be
evaluated via direct transfer on several target institutions.

Voting Transfer: This training paradigm uses a form of averaging to combine
the results of models (“voters”) trained on disjoint distributions. In our
experiments, none of the voters are trained on the target institution, which
mimics the case where an institution without any historical training data uses
a set of models from other institutions in a zero-shot scenario. The model
under the voting transfer paradigm for target institution $i$ is defined by
$\frac{1}{c}\sum_{i^{\prime}\in\mathcal{I}\setminus
i}f(\hat{\theta}(\mathcal{D}_{i^{\prime}}),\cdot)$, where $c$ is the
normalizing constant $|\mathcal{I}|-1$. Note that this model does not use
majority voting, but instead uses “soft voting,” where the predicted
probabilities (not the decisions) of each model are aggregated with equal
weight. This allows for the confidence of each model to be taken into account
in the aggregation.999The choice of equal weighting is by convention; in
practice, any combination of weights on the $(\mathcal{I}-1)$-simplex could be
used to aggregate the predictions of the voters. This weight vector could also
be tuned on the target institution in a non-zero-shot formulation.

Stacked Transfer: This training paradigm uses stacked generalization (Wolpert,
1992; Ting and Witten, 1997) to combine the predictions of models trained on
all available institutions with the training data of the source institution.
This is achieved by concatenating, for each input $x_{i}$, the predictions of
each classifier $f(\hat{\theta}(X_{j}),x_{i})$, to the input features, and
learning a classifier from this concatenated data matrix. Formally, for
institution $\ell$, if we define

(1)
$\check{x}=[x_{1},...,x_{d};f(\hat{\theta}(\mathcal{D}_{i},x);f(\hat{\theta}(\mathcal{D}_{j},x);f(\hat{\theta}(\mathcal{D}_{k},x)]$

where $[\cdot;\cdot]$ indicates column-wise concatenation, then the stacked
estimator is $f(\hat{\theta}(\check{X}))$.

Because the final two forms of transfer (voting transfer, stacked transfer)
are both methods for ensembling, we refer to these two methods collectively as
ensemble models.

###  4.4. Metrics

Metrics for evaluating various aspects of model fairness have been proposed in
prior work (see Section 2). However, many of these metrics are based on the
implicit or explicit assumption that one outcome is advantageous or favorable,
and that a “fair” model can ensure some form of equity with respect to the
model’s predictions in placing members of sensitive subgroups into the
favorable outcome class. This is often tied to contexts in which the model’s
predictions may be explicitly tied to some form of decision (e.g., granting a
loan). Our task differs from these contexts, because the model is not
explicitly tied to a decision but instead provides a prediction that might be
used to assist a student, but is only useful when correct—neither predictive
outcome is considered inherently “advantageous.” In our application, the goal
of the model is to obtain equal predictive performance for all subgroups,
regardless of the true or predicted outcome. We call this equitable predictive
performance. This makes many existing fairness metrics, such as demographic
parity, which assume the presence of an advantageous outcome to which we would
like to equitably assign predictions, not applicable to the dropout prediction
task. There are many tasks where equitable predictive performance is desired,
such as machine translation, where consistent performance is desired across
dialects or languages despite differing availability of training data (Ahia et
al., 2021), and image classification with respect to skin tone or other
attributes (Buolamwini and Gebru, 2018).

Educational dropout data tends to be highly skewed by label, because in many
institutional contexts, the majority of students do not drop out. This is the
case in our data as well: the retention rate in our universities varies from
56% (Institution B) to 98% (Institution D; see Table 1). As a result, metrics
such as average accuracy will tend to be biased toward majority-class
predictors and will be uninformative for the small but critical subset of
students who drop out.

Area Under the Receiver Operating Characteristic Curve (AUC): Due to our goal
of equitable prediction and the significant label imbalance in our datasets,
our experiments use metrics based on the Area Under the Receiver Operating
Characteristic Curve (AUC), formally defined as:

(2) $AUC(f(\theta))=\int_{0}^{1}\textrm{TPR}(\textrm{FPR}(f_{t}(\theta)))dt$

where $t$ indicates a prediction threshold applied to the predictions of the
model (i.e. using the decision rule
$f_{t}(\theta,x)=\mathbbm{1}\big{(}f(\theta,x)\geq t\big{)}$), and TPR, FPR
are the true positive rate and false positive rates, respectively. AUC scores
are constrained to $[0,1]$, with a random predictor achieving an AUC of 0.5.
In all metrics and experiments, we compute the AUC on the test dataset,
following the splitting process described in Section B.2.

AUC is a well-studied metric of predictive performance (Bradley, 1997; Hanley
and McNeil, 1982; Japkowicz and Shah, 2011), and has the straightforward
interpretation as the probability that a randomly-selected positive example
has a higher predicted probability of being positive than a randomly-selected
negative example. This means that the positive and negative classes are
equally weighted in computing AUC, and that AUC is less rewarding to, for
example, majority-class predictors than metrics such as accuracy or cross-
entropy loss. We compute standard errors for AUC values according to the
procedure described in (Hanley and McNeil, 1982; Fogarty et al., 2005). We
provide details on computing these standard errors in Section E.

AUC Gap: To measure fairness across subgroups, we define a metric that
accounts for the disparities in predictive performance across a set of
arbitrarily many (possibly-overlapping) subgroups $\mathcal{G}$. We define the
AUC Gap as:

(3)
$\textrm{max}_{g,g^{\prime}\in\mathcal{G}}~{}~{}|\mathbb{E}_{\mathcal{D}_{k}}[f(\theta(\mathcal{D}_{k,g})]-\mathbb{E}_{\mathcal{D}_{k}}[f(\theta(\mathcal{D}_{k,g^{\prime}})]|$

where $\mathcal{D}_{k,g}$ and $\mathcal{D}_{k,g^{\prime}}$ indicate the subset
of the data in group $g$ and $g^{\prime}$, respectively. Thus, AUC Gap
measures the largest difference between subpopulation AUCs, and is a measure
of the worst-case performance gap between a set of subpopulations. AUC Gap is
our primary measure of equitable predictive performance, because it quantifies
the largest disparity in predictive performance over subgroups.

$\Delta$AUC: We define $\Delta$AUC to measure changes in predictive
performance or fairness under cross-institutional transfer. We define the
change in AUC between two transfer contexts for a fixed model $f$, as $\Delta
AUC(T,T^{\prime})=AUC(T)-AUC(T^{\prime})$ where, somewhat abusing notation, we
use $AUC(T)$ to refer to the AUC of a model trained using a transfer scheme
$T$. This allows us to compare, for example, how (overall or subgroup) AUC
values are affected by transfer learning schemes. If $\Delta\textrm{AUC}$ is
close to zero, we can conclude that the model performs about the same in two
transfer contexts; but if it is positive or negative, the model performs
better/worse in context $T^{\prime}$ relative to $T$. Most often in this
study, we are interested in $\Delta\textrm{AUC}$ relative to the local model;
that is, $\Delta\textrm{AUC}(\textrm{local},\cdot)$.

##  5\. Experimental Setup

Parameterization and Tuning of $f$: We evaluate three forms of model transfer
learning (_direct transfer_ , _voting transfer_ and _stacked transfer_ ,
described previously) plus _local_ models on our four institutional datasets.
For each experiment, we explore three parameterizations of $f$: $(1)$
$L_{2}$-regularized logistic regression (L2LR); $(2)$ gradient-boosted trees
(LightGBM (Ke et al., 2017)); $(3)$ neural networks (multilayer perceptrons).
Below, we primarily focus on L2LR in the main text due to space constraints,
because (1) we observed the best performance for L2LR models across transfer
schemes; (2) L2LR models are the simplest to train and tune, even for
institutions with low capacity for data science and modeling; and (3) L2LR
models are highly interpretable and widely used for student retention models
in practice (see Section 2.1). We provide the complete results for other
models in the supplementary material, including a parallel version of each
figure in the main text for the other models (LightGBM, MLP); our findings
with L2LR are consistent with our findings for these other models, except
where explicitly noted.

Hyperparameters of each model are tuned locally via cross-validation on the
source institution, and complete hyperparameter grids for each model are
provided in our associated source code. For stacked models, the stacked
model’s hyperparameters are also tuned via cross-validation. A subset of the
training data is held out and used only as a validation set for model
selection (see below). The trained models are always evaluated on the test
data from each institution, which is from a future academic term (see Section
B.2 for details).

As noted previously, _voting transfer_ is a form of zero-shot transfer and
demonstrates how an institution with no training data might make use of models
from other institutions. Voting transfer experiments do not use the base model
from the target institution and do not require any training on the target
institution: they simply use weighted majority voting to aggregate the results
of each trained source model. Voting transfer allows us to evaluate the zero-
shot transfer of models to an institution with no training data available.

Model Selection Rules: For the stacked transfer experiments, we explore the
use of all three functional forms mentioned above (i.e. the stacked model can
be L2LR, LightGBM, or MLP). However, it is not clear how the choice of base
learners used to construct the stacked ensemble affects the (accuracy,
fairness) of the downstream stacked model, particularly when multiple base
models are available from each institution – a realistic scenario, as it is
not uncommon for an institution to train and evaluate many models during the
development phase. Furthermore, it is possible that a “greedy” approach to
selecting the base models may have unintended consequences for performance
(for example, the best-performing model at Institution A may lead to poor
performance when used in an ensemble at Institution C). We therefore conduct a
principled investigation comparing four strategies for selecting which trained
models to include in the stacking process, as follows. First, in addition to
training the cross-validated models tuned at each institution, we train $10$
additional models of each type (L2LR, LightGBM, MLP) with a fixed set of
hyperparameters, varying only the $L_{2}$ regularization of each model over a
large grid. Second, from this pool of 11 candidate models at each institution
(one cross-validated model plus 10 models with various degrees of
regularization), we apply one of four _model selection rules_ to choose which
estimators are included to construct (1). Finally, we fit the stacked model
and evaluate it on the target institution (the base learners are frozen
throughout this process). We explore the following model selection rules:

  * •

Best Performance: only the model with the best validation AUC at each
institution is used.

  * •

Best Fairness: only the model with the best validation AUC Gap (Equation (3))
is used.

  * •

Same Family: the cross-validated models of the same functional form are used
(e.g. LightGBM).

  * •

Kitchen Sink: all 11 models are used.

Due to space constraints, our results in the main text reflect the best
performance selection rule, as this is the approach most commonly used in
practice. We provide additional results for all model selection rules in
Section D.4 (e.g. Figure 6).

##  6\. Results

###  6.1. Overall Predictive Performance of Cross-Institutional Transfer
Models

Figure 2. (a) Left: Predictive performance on test data for various transfer
schemes evaluated. (b) Right: $\Delta$AUC values for various transfer models
evaluated with the _local_ model reference line. 95% confidence intervals
shown for both figures; text displays values for point estimates. (See also
Figure 8 and Table 3).

In RQ1 we are concerned with measuring model performance across three
different transfer schemes (direct, voting, and stacked). Figure 2a shows the
AUC for models using each transfer scheme, as well as the performance of
direct transfer of models from a given source institution to a target
institution, for each of the four institutions in our study.
$\Delta\textrm{AUC}$ values for each transfer scenario are shown in Figure 2b.

Direct Transfer Models: Our results in Figure 2 show that direct transfer has
inconsistent performance: for two of four institutions (B and D), all direct
transfer models achieve indistinguishable performance from local models (as
indicated by $\Delta\textrm{AUC}=0$ confidence intervals covering zero in
Figure 2b for direct transfer models); for the remaining two institutions (A
and D), the results are mixed. This suggests, perhaps unsurprisingly, that
direct transfer of models may sometimes achieve good overall performance
(compared to a local model), but not in all cases.

Ensemble Models (Voting Transfer and Stacked Transfer): Figure 2 shows results
with respect to voting and stacked transfer models. These results for both
voting transfer and stacked transfer are consistent across all institutions in
our study.

In our experiments, zero-shot voting transfer achieves similar performance to
local models (as indicated by $\Delta\textrm{AUC}=0$ confidence intervals
covering zero in Figure 2b for voting transfer models). These results suggest
that all institutions can obtain models with equivalent performance to a local
model by performing zero-shot weighted aggregation of a set of models trained
only on other institutions.

Furthermore, stacked transfer provides no additional benefit over local models
(or zero-shot models). Figure 2a shows that stacked transfer models do not
improve over either local models or voting transfer models (as indicated by
overlapping confidence intervals for AUC between stacked and local/voting
models in Figure 2a). This suggests that once institutions have leveraged
_either_ their own local training data (local model) _or_ other institutions’
models (voting transfer), combining these information sources (via stacked
model) provides no additional performance gains in our experiments.

A $z$-test confirms that $\Delta\textrm{AUC}(\textrm{local},\textrm{voting})$
and $\Delta\textrm{AUC}(\textrm{local},\textrm{stacked})$ are statistically
indistinguishable from zero at $\alpha=0.05$ (all $p>0.1$), suggesting that
the voting ensemble method is an effective way to reduce uncertainty over
which direct transfer model should be used when no local training data is
available, but that stacking provides no additional performance gains. We
provide exact $p$-values for the hypothesis test that
$H_{0}:\Delta\textrm{AUC}\neq 0$ in supplementary Table 3. This suggests, in
particular, that zero-shot transfer of a voting ensemble of three other
institutions can achieve performance statistically indistinguishable from a
locally-trained model.

###  6.2. Intersectional Fairness Analysis of Cross-Institutional Transfer
Models

Figure 3. (a) Left: Intersectional performance over all sensitive subgroups
for various transfer schemes evaluated. (b) Right: Fairness metric AUC gap
over intersectional sensitive subgroups for various transfer schemes
evaluated. 95% confidence intervals shown; text displays values for point
estimates. Note that the AUC gap (b) is the range of these values within each
institution (shown as vertical bar in (a)). (See also Figures 9(a), 9(b),
Table 4.)

Our fairness analysis evaluates whether transferred models achieve equivalent
predictive performance over sensitive subgroups. A substantial body of work
across many disciplines and dating back several decades delineates how the
intersections of individuals’ identities can contribute to disempowerment and
increase vulnerability to adverse outcomes (EISESTEIN, 1979; Crenshaw, 1989;
Truth, 1851). In machine learning, however, most prior work on fairness
focused on analyzing one sensitive attribute at a time (notable exceptions
include (Foulds et al., 2019; Morina et al., 2019; Yang et al., 2020)),
despite the frequent presence of multiple potentially sensitive attributes in
a dataset. Therefore, we measure fairness across intersectional subgroups via
AUC Gap defined in Section 4.4. For sensitive attributes
$a\in\mathcal{A}_{1},a^{\prime}\in\mathcal{A}_{2}$, we compute each metric
$\mathcal{L}$ on the subset
$\mathcal{D}_{a,a^{\prime}}\coloneqq(x_{i},y_{i}|A_{1}(x)=a,A_{2}(x)=a^{\prime})$.
Each metric is therefore computed as
$\mathcal{L}\big{(}f(\hat{\theta}(\mathcal{D}),\tilde{X}_{a,a^{\prime}}),\tilde{y}_{a,a^{\prime}}\big{)}$.
By evaluating fairness in this way, our analysis captures whether changes in
AUC are distributed equally over (observable) intersecting student identities,
“focus[ing] awareness on people and experiences—hence, on social forces and
dynamics—that, in monocular vision, are overlooked” (MacKinnon, 2013).

We specifically use this approach to examine subgroups of students defined by
sex and URM status. These represent two critical identities in the context of
education with respect to which unfairness is undesirable but common in
educational settings. We compute evaluation metrics for intersections of
$\mathcal{A}_{1}=\\{\textrm{male},\textrm{female}\\}$ for Sex and
$\mathcal{A}_{2}=\\{\textrm{Underrepresented Minority},\textrm{Non-
Underrepresented Minority}\\}$ for URM.101010Most institutions recorded more
than two categories for Sex, but these tended to be ”other” and ”not
indicated”, and besides making up a small share of students, it was unclear
how these responses were collected in order to interpret them correctly and
consistently. We do not endorse the terminology or definition of URM; we only
use it because it is consistently defined across institutions to abide by
federal regulations. The main results of our fairness analysis are shown in
Figures 3 and 4; we also provide detailed data in supplementary Table 4.
Below, we address RQ2 by separately discussing these disparity metrics under
each transfer approach.

Before reporting the results, we raise two issues related to fairness,
accountability, and transparency. First, the data we use is what institutions
make available, and does not encapsulate all potential identities related to
the sex or gender construct, and thus there is _measurement bias_ inherent in
the data. Second, AUC (and related metrics, such as F1 score) cannot be
computed unless there is at least one positively-labeled and negatively-
labeled observation in each subgroup, and our data did not include any other
intersectional groups where this precondition was not satisfied, and thus
fairness for other measures was not evaluated, a form of _algorithmic bias_.

Local and Direct Transfer Models: Figure 3a presents the four intersectional
subgroup AUCs underlying the computation of each AUC gap, which is summarized
in Figure 3b. The results in Figure 3 show that local and direct transfer
models do not differ in their performance disparities over subgroups as
measured by AUC gap (Equation (3)). There is no consistent difference between
the subgroup performance disparities of local vs. direct transfer models in
our study, and in no case can we reject
$H_{0}:\Delta\textrm{AUC}(\textrm{local},\textrm{direct})=0$. Figure 3a also
shows that a single intersectional subgroup often drives the observed
performance disparities, which persist across different source models: for 17
of 24 transfer schemes evaluated, the Female Non-URM group is the lowest-AUC
group for the model.

Ensemble Models (Voting Transfer and Stacked Transfer): In general, ensemble
models achieve similar fairness relative to a local model across our
experiments. Figure 5b shows that, for all institutions, both voting transfer
and stacked transfer achieve confidence intervals for $\Delta\textrm{AUC}$
that overlap with the local model. Particularly for the voting transfer model,
this is an encouraging result: It suggests that the practical benefits from
the use of zero-shot voting transfer (achieving performance equivalent to a
local model, _without_ having local training data; see Section 6.1) do not
come at a cost to fairness, an important result. It also suggests that the
improvements of voting transfer over direct transfer models do not benefit
only one group; instead, the gap between the min and max AUC groups stays the
same while the overall AUC improves under voting transfer (relative to direct
transfer).

For 20 of 24 transfer schemes evaluated, we reject
$H_{0}:\Delta\textrm{AUC}=0$ (see Table 4 for details). This means that for
most models, there is a nonzero gap between the best- and worst-performing
groups for the learned model. This suggests that future work is needed to
improve performance for some intersectional groups if equivalent performance
across groups is possible and desirable.

###  6.3. Exploratory Findings

This section discusses exploratory findings from our study. Our large-scale
empirical study, being the first of its kind in the domain of higher
education, is uniquely positioned to provide empirical insight into several
questions of interest. However, as a purely observational study with a limited
set of institutions, it is our intention to clearly position our discussion of
the following findings as _exploratory_ : our study provides initial evidence,
but does not _prove_ there is a relationship, particularly a causal
relationship, between the factors discussed here.

No tradeoff between fairness and accuracy: RQ3 in our study concerns whether
there is a tradeoff between fairness and accuracy in cross-institutional
transfer. Our results suggest that the variation in AUC Gap is epxlained by
other factors (namely, institution and the transfer type), and that AUC Gap is
_not_ associated with AUC after controlling for these factors. We explore a
simple linear regression of AUC Gap on AUC, with terms for the target
institution and the transfer type. We find that in the resulting linear model,
the AUC term $\beta_{\textrm{AUC}}$ has $t=-0.350$ ($p=0.72719$), suggesting
that we do _not_ have evidence to suggest that AUC and AUC Gap are associated,
after controlling for the target institution and transfer type. We show a
scatter plot of the data used to conduct this analysis in supplementary Figure
11, and provide details on the model, in Section D.

Impact of Intersectional Analysis: In Section D.3, we briefly compare the
findings of our intersectional analysis with a non-intersectional (“marginal”)
analysis. This comparison demonstrates that marginal analyses are more likely
to ignore performance disparities within subgroups, and to assign lower
overall AUC Gap scores to models.

No clear impact of regularization: We also study whether effective
regularization helps reduce subgroup performance disparities. One potential
interpretation of the disparities measured by AUC Gap might be that models
simply overfit to certain groups; in this case, effectively tuning the
regularization parameter might reduce the degree of overfitting to certain
groups. To investigate the impact of regularization, we conduct a sweep of the
$L_{2}$ regularization for all models (L2LR, LightGBM, MLP; all contain an
$L_{2}$ regularization term) and keep all other hyperparameters at default
values. We provide the results of this study in Figure 10, and give further
detail on the design of these experiments in Section D.6. Our results suggest
that there is not a clear relationship between regularization and AUC Gap.
This aligns with existing work on subgroup robustness, which suggests that
subgroup performance tends to improve along with the overall model (in which
case regularization should be tuned to optimize the bias-variance tradeoff)
(Gardner et al., [n. d.]).

##  7\. Conclusion

This paper presents the first large-scale empirical study of model performance
and fairness in cross-institutional transfer learning. We proposed a set of
metrics for quantifying cross-institutional transfer performance and fairness,
and applied those techniques in the context of university student dropout
prediction with real-world education data. Our results show that cross-
institutional transfer is possible, where even zero-shot “voting transfer”
models achieve statistically indistinguishable performance to a local model
with no change in intersectional subgroup fairness. Additionally, our results
show more broadly that there is no evidence of a performance-fairness tradeoff
across a wide scope of functional forms (L2LR, LightGBM, MLP), transfer
schemes (direct, voting, stacked), and selection rules for the ensemble
components (best performance, best fairness, same family, kitchen sink).

These findings have important implications for both researchers and
practitioners. For machine learning researchers, the demonstrated success of
relatively simple approaches (e.g. voting transfer) suggests that further
investigation is needed to understand the conditions under which $(i)$ zero-
shot transfer is effective, and $(ii)$ more sophisticated transfer learning
and ensembling methods succeed or fail. For educational researchers, the
results suggest that while institutional contexts matter in understanding and
predicting student dropout, there exists a decent level of generalizable
knowledge that can facilitate the development of portable predictive models.
For practitioners, our results show that the cross-institutional learning
paradigm can serve as a viable means for well-resourced institutions to
support their underresourced counterparts. This is especially relevant in an
era with growing availability of big data and increasing prevalence of
algorithmic decision making.

On the other hand, this study has a handful of limitations. First, our models
are trained on available data from each institution, which could contain their
own biases (Barocas et al., 2019; Kizilcec and Lee, 2022). Treating
institutional datasets as a source of truth masks complexities in how
variables are coded and in how historical inequities are manifested in the
data, which could affect the applicability of our conclusions. Second, our
sample only includes four institutions in the United States that have the data
infrastructure and capacity to make large-scale data available for research.
This limits the generalizability of our results to other institutions with
varying degrees of similarity in student populations and dropout-generating
processes. The breadth of cultural perspectives in non-U.S. contexts, as well
as the definition of which students are under-represented, also suggest a need
for replication and extension of this work.

Informed by the limitations, there are a few lines of future work. First,
further studies on cross-institutional transfer are needed, including similar
studies in education and other decentralized organizations with large-scale
shared electronic record-keeping systems (e.g., hospitals, local governments,
financial institutions). Future work should evaluate additional transfer
approaches and could include the development of algorithms designed explicitly
to mitigate performance disparities. Second, cross-institutional collaborative
modeling is still difficult, due to a combination of data-sharing restrictions
and a lack of technical infrastructure for cross-institutional collaboration
with private data. We encourage the development of better technical and
theoretical frameworks for collaborative learning in the presence of strict
data-sharing constraints. Finally, our work suggests that overall performance
can be improved without a strict cost to fairness, providing a motivation for
further improvement of general classification techniques for student retention
modeling, even without explicit disparity-mitigating interventions.

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##  Appendix A Acknowledgements

This research was partly funded by a Google gift via the 2021 Award for
Inclusion Research program. Josh Gardner was supported by a grant from
Microsoft.

##  Appendix B Data

###  B.1. Schema

The complete schema for the institutional data used in this study is shown in
Table 2. As discussed in Section 4.1, the data is extracted from each
institution’s student information system (SIS), and is a subset of the data
available at each institution. These variables were chosen based on a
combination of availability, expected predictive utility (based on prior
research discussed in Section 2.1 and the researchers’ own experience), and
consistency of coding across institutions.

Feature Name |  Description | Type |  | Nullable | Min | Max | Student | Multiple Columns
---|---|---|---|---|---|---|---|---
Units |  Credit units the student enrolled in in this term | Float |  |  | 0 | 100 |  |
Units Failed |  Percentage of enrolled units the student failed | Float |  |  | 0 | 100 |  |
Units Incomplete |  Percentage of enrolled units the student earned an incomplete for | Float |  |  | 0 | 100 |  |
Units Withdrawn |  Percentage of enrolled units the student withdrew from | Float |  |  | 0 | 100 |  |
Cumulative GPA |  Cumulative GPA from all known tertiary education sources | Float |  |  | 0 | 4 |  |
Units Transferred |  Total number of transferred units in this term | Integer |  | ✓ | 0 | 100 | ✓ |
Age |  Age at course start | Integer |  | ✓ | 0 | 150 | ✓ |
High School GPA |  GPA in high school | Float |  | ✓ | 0 | 4 | ✓ |
ACT English |  ACT English component score | Integer |  | ✓ | 0 | 36 | ✓ |
ACT Math |  ACT Math component score | Integer |  | ✓ | 0 | 36 | ✓ |
SAT Math |  SAT Math component score | Integer |  | ✓ | 0 | 800 | ✓ |
SAT Verbal |  SAT Verbal component score | Integer |  | ✓ | 0 | 800 | ✓ |
GPA Mean |  The term-level gpa average weighted by units | Float |  |  | 0 | 4 |  |
GPA Stddev |  The term weighted gpa stddev | Float |  |  | 0 | inf |  |
GPA $z$-score |  The weighted average z-score of the student in their courses | Float |  |  | -inf | inf |  |
GPA $z$-score stddev |  The weighted stddev z-score of the student in their courses | Float |  |  | 0 | inf |  |
Units Per CIP2 |  Units taken by 2-digit CIP code | Float |  |  | 0 | 100 |  | ✓
Units Per Course |  Units taken by course format | Integer |  |  | 0 | 100 |  | ✓
Units Online |  Units taken online. | Integer |  |  | 0 | 100 |  |
Units In-Person |  Units taken in person. | Integer |  |  | 0 | 100 |  |
Modality |  Whether the student is enrolled in-person or online | Categorical |  |  |  | ✓ |  |
Sex |  Self-declared sex | Categorical |  |  |  |  | ✓ |
Ethnicity |  Self-declared ethnicity | Categorical |  |  |  |  | ✓ |
URM Status |  Institutionally-assigned indicator for underrepresented minority status | Categorical |  |  |  |  | ✓ |
Major 1 CIP Code |  2-digit CIP code for first major | Categorical |  |  | 1 | 61 | ✓ |
Major 2 CIP Code |  2-digit CIP code for second major | Categorical |  |  | 1 | 61 | ✓ |
Minor 1 CIP Code |  2-digit CIP code for first minor | Categorical |  |  | 1 | 61 | ✓ |
Minor 2 CIP Code |  2-digit CIP code for second minor | Categorical |  |  | 1 | 61 | ✓ |
Year |  The current year | Integer |  |  | 2013 | 2019 | ✓ |
Retention |  Indicator for whether student was enrolled in following fall term | Binary |  |  | 0 | 1 | ✓ |
Table 2. Data schema used for this study. Each row in the resulting dataset
represents a single first-year student present in the Fall academic term at an
institution. “Student-level” features indicate those which are fixed for a
given student under normal circumstances, and do not vary by term. For more
detail on categorical codings and handling of nullable features, see Section
B.1 Note that min/max values indicate the min/max enforced by our data
validation pipeline; these are not the min/max values occurring in the data
(which often fall into a much smaller range).

The “CIP2 code” referenced in Table 2 refers to the Classification of
Instructional Programs (CIP) codes defined by the Center for Educational
Statistics111111https://nces.ed.gov/ipeds/cipcode/. CIP codes are written as
decimal values (i.e. 14.43 is the CIP code for “Biochemical Engineering”). We
use the “coarse” CIP codes, which are represented by the integer value
preceding the decimal (i.e. 14 represents “Engineering”). A complete list of
CIP codes may be viewed at https://nces.ed.gov/ipeds/cipcode/browse.

For features marked as “multicolumn” in Table 2, several identical features
are generated to represent the information for that row. For example, for
“Units Per Course Type”, we generate 62 features, where each feature indicates
the number of units associated with a given CIP code (1-61, or “Missing” when
the CIP code is not available).

The “Retention” variable indicates the prediction target for this study, and
is an indicator for whether the student was enrolled in the following fall
term, according to the university’s enrollment records. Note that this is only
a 1-year measure of retention; it does not measure whether the student
persists to complete a degree.

Additional categorical variables are coded as follows:

  * •

Course Component: a variable indicating which “component” of a course an
individual record is assigned to (note that courses may sometimes also consist
of multiple components, such as a lecture and a lab component). These also
include multiple-component courses, which are simply the set of all
combinations of the following course components: Lecture, Discussion, Lab,
Seminar, Other.

  * •

Sex: a self-declared variable representing the students’ declared sex or
gender identity. The procedure for collecting this data, along with the exact
allowed values, vary by institution; we include the following possible values,
but recognize the limitations of such a coding: Male, Female”, Not Indicated,
Other.

  * •

Ethnicity: a self-declared variable representing the students declared
ethnicity. The procedure for collecting this data, along with the exact
values, vary by institution. As above, we include the following possible
values, which reflect the union of categories across our institutions, but
recognize the limitations of this coding: Asian, Black, Hawaiian, Hispanic,
Native American, Not Indicated, White, 2 or More.

  * •

URM Status: The term ‘Underrepresented Minority’ holds a specific
institutional meaning in higher education, where it is used to refer to a
category of domestic students (those with U.S. citizenship status) who hold
membership in an underrepresented racial or ethnic group in the United States.
We note that this is a category that is tracked and reported by almost every
accredited institution in the United States. As a result, we decided to
include this variable, instead of deriving a potentially more socially
meaningful, but less contextual, “underrepresented minority” feature. This
variable takes the following values: Non-Underrepresented Minority,
Underrepresented Minority, International.

For variables marked as “nullable” in Table 2, handle them in two distinct
ways: for some variables (high school GPA, ACT English, ACT Math), we drop
records with those values not present (since missingness is rare for these
features). For the remaining nullable features (SAT Math, SAT Verbal) we use
median imputation.

We note that for all institutions, we only use records up to the Fall 2019
term in order to avoid forecasting into the academic terms affected by the
COVID-19 crisis.

###  B.2. Train/Test/Validation Split

Our goal is to realistically evaluate models’ ability to predict on future
data. To do so, we use as training data records from all terms prior to Fall
2019 term. We reserve all records from the Fall 2019 term as
validation/testing data, where these records are split evenly into
test/validation.

##  Appendix C Open-Source Code Release

Concurrent to the release of this paper, we will make our code publicly
available via public GitHub repository. This includes code for data
validation, model training, and evaluation, as well as other reproducibility
details (software requirements, code for generating figures).

##  Appendix D Additional Results

###  D.1. Transfer Gap $\Delta\textrm{AUC}$ Detailed Results

We provide detailed experimental results for the transfer gap measure
$\Delta\textrm{AUC}$ in Table 3, and detailed experimental results for the AUC
Gap fairness measure in Table 4.

Target
Institution |  Source
Institution(s) | $\Delta\textrm{AUC}$ | $\textrm{SE}(\Delta\textrm{AUC})$ | Transfer Type | $p$
---|---|---|---|---|---
A |  D-C-B | $-0.021\,999\,659\,521\,627\,9$ | $0.016\,320\,408\,677\,740\,9$ | Majority Voting | $0.177\,663\,336\,630\,349$
A |  D-C-A-B | $0.010\,407\,122\,006\,418\,9$ | $0.015\,611\,166\,523\,864\,2$ | Stacked | $0.504\,998\,267\,250\,98$
A |  D | $-0.056\,518\,158\,012\,007$ | $0.017\,030\,094\,040\,009\,4$ | Direct |  $0.000\,904\,302\,137\,413\,95$*
A |  C | $-0.015\,054\,902\,137\,503\,3$ | $0.016\,171\,599\,698\,859\,4$ | Direct | $0.351\,880\,983\,453\,849$
A |  B | $-0.018\,997\,942\,108\,662\,7$ | $0.016\,256\,318\,917\,034$ | Direct | $0.242\,544\,798\,336\,53$
B |  D-C-A | $0.024\,590\,163\,934\,426\,1$ | $0.062\,133\,341\,708\,087\,1$ | Majority Voting | $0.692\,278\,850\,800\,52$
B |  D-C-A-B | $0.026\,127\,049\,180\,327\,8$ | $0.062\,056\,601\,112\,768\,1$ | Stacked | $0.673\,740\,724\,900\,487$
B |  D | $-0.040\,983\,606\,557\,377\,1$ | $0.064\,976\,665\,442\,248\,5$ | Direct | $0.528\,208\,279\,850\,642$
B |  C | $0.004\,098\,360\,655\,737\,65$ | $0.063\,112\,299\,255\,056\,8$ | Direct | $0.948\,223\,690\,710\,095$
B |  A | $-0.021\,772\,540\,983\,606\,6$ | $0.064\,230\,769\,249\,110\,4$ | Direct | $0.734\,629\,548\,960\,961$
C |  D-A-B | $-0.049\,532\,501\,472\,569\,6$ | $0.029\,772\,095\,240\,024\,7$ | Majority Voting | $0.096\,167\,919\,562\,402\,5$
C |  D-C-A-B | $0.005\,714\,247\,026\,086\,36$ | $0.028\,134\,111\,705\,290\,4$ | Stacked | $0.839\,051\,067\,183\,201$
C |  D | $-0.042\,697\,747\,476\,320\,5$ | $0.029\,581\,361\,237\,227\,8$ | Direct | $0.148\,907\,722\,595\,508$
C |  A | $-0.094\,241\,068\,103\,804\,4$ | $0.030\,926\,254\,384\,457$ | Direct |  $0.002\,309\,197\,212\,896\,36$*
C |  B | $-0.079\,044\,827\,049\,241\,4$ | $0.030\,552\,800\,337\,230\,6$ | Direct |  $0.009\,677\,207\,839\,214\,69$*
D |  C-A-B | $0.003\,324\,447\,712\,718\,56$ | $0.065\,907\,791\,319\,253\,5$ | Majority Voting | $0.959\,771\,051\,599\,402$
D |  D-C-A-B | $-0.000\,199\,160\,462\,052\,483$ | $0.066\,159\,087\,033\,920\,5$ | Stacked | $0.997\,598\,110\,480\,144$
D |  C | $0.013\,067\,990\,317\,737\,4$ | $0.065\,203\,806\,208\,683\,2$ | Direct | $0.841\,153\,996\,313\,111$
D |  A | $-0.038\,790\,329\,993\,565\,7$ | $0.068\,785\,006\,447\,145\,2$ | Direct | $0.572\,797\,801\,583\,429$
D |  B | $0.018\,950\,883\,966\,050\,7$ | $0.064\,772\,567\,526\,943$ | Direct | $0.769\,846\,434\,720\,799$
Table 3. Detailed results for transfer gap $\Delta\textrm{AUC}$ for each
transfer scheme evaluated. The final column gives the $p$-value of the
hypothesis test of $\Delta\textrm{AUC}\neq 0$ for the transfer scheme
evaluated. $*$ indicates we reject $H_{0}$ at $\alpha=0.05$. Target
Institution |  Source
Institution(s) | AUC Gap | SE(AUC Gap) | Transfer Type | p
---|---|---|---|---|---
A |  D-C-B | $0.122\,147\,108\,408\,432$ | $0.033\,883\,871\,269\,350\,2$ | Majority Voting |  $0.000\,312\,303\,633\,993\,873$*
A |  D-C-A-B | $0.157\,333\,514\,580\,536$ | $0.032\,092\,300\,021\,146\,8$ | Stacked |  $9.460\,939\,563\,410\,77\text{\times}{10}^{-07}$*
A |  B | $0.109\,405\,527\,669\,79$ | $0.033\,717\,145\,007\,173\,5$ | Direct |  $0.001\,175\,314\,817\,576\,19$*
A |  C | $0.143\,255\,245\,996\,841$ | $0.034\,274\,205\,675\,720\,8$ | Direct |  $2.919\,183\,065\,755\,32\text{\times}{10}^{-05}$*
A |  D | $0.138\,921\,799\,024\,389$ | $0.035\,992\,171\,645\,772\,1$ | Direct |  $0.000\,113\,489\,993\,898\,567$*
A |  A | $0.140\,084\,010\,749\,891$ | $0.032\,257\,065\,833\,260\,7$ | Direct |  $1.407\,174\,112\,166\,76\text{\times}{10}^{-05}$*
B |  D-C-A | $0.255\,265\,567\,765\,568$ | $0.102\,071\,050\,725\,772$ | Majority Voting |  $0.012\,389\,159\,582\,966\,9$*
B |  D-C-A-B | $0.307\,800\,043\,094\,161$ | $0.090\,812\,988\,233\,025\,7$ | Stacked |  $0.000\,700\,499\,695\,884\,281$*
B |  A | $0.356\,410\,256\,410\,256$ | $0.191\,266\,473\,105\,912$ | Direct |  $0.062\,402\,841\,780\,543\,4$*
B |  C | $0.240\,600\,086\,188\,322$ | $0.104\,682\,616\,396\,358$ | Direct | $0.021\,540\,358\,586\,244\,2$
B |  D | $0.286\,104\,826\,546\,003$ | $0.116\,851\,763\,491\,944$ | Direct |  $0.014\,347\,531\,962\,017\,9$*
B |  B | $0.311\,339\,009\,287\,926$ | $0.095\,514\,382\,117\,890\,3$ | Direct | $0.001\,115\,680\,853\,690\,03$
C |  D-A-B | $0.083\,418\,737\,557\,264\,9$ | $0.067\,748\,691\,277\,526\,4$ | Majority Voting | $0.218\,211\,929\,157\,495$
C |  D-C-A-B | $0.121\,194\,472\,162\,624$ | $0.057\,068\,054\,499\,966\,8$ | Stacked | $0.033\,696\,637\,897\,166\,3$
C |  A | $0.187\,121\,457\,321\,451$ | $0.067\,013\,464\,399\,495\,9$ | Direct |  $0.005\,233\,538\,712\,527\,54$*
C |  B | $0.105\,083\,255\,068\,609$ | $0.075\,456\,526\,426\,783\,6$ | Direct | $0.163\,730\,773\,340\,565$
C |  D | $0.092\,819\,327\,822\,257$ | $0.070\,739\,629\,536\,824\,1$ | Direct | $0.189\,477\,526\,093\,772$
C |  C | $0.121\,227\,004\,351\,214$ | $0.057\,514\,941\,917\,109\,2$ | Direct |  $0.035\,052\,792\,115\,160\,3$*
D |  C-A-B | $0.363\,635\,955\,988\,274$ | $0.115\,238\,014\,052\,529$ | Majority Voting | $0.001\,602\,118\,152\,406\,61$
D |  D-C-A-B | $0.326\,687\,906\,724\,512$ | $0.116\,687\,747\,416\,188$ | Stacked | $0.005\,115\,389\,377\,678\,55$
D |  A | $0.492\,050\,042\,178\,838$ | $0.123\,445\,420\,972\,504$ | Direct |  $6.720\,432\,117\,589\,81\text{\times}{10}^{-05}$*
D |  B | $0.328\,156\,966\,935\,154$ | $0.108\,867\,147\,434\,087$ | Direct |  $0.002\,575\,829\,207\,022\,48$*
D |  C | $0.344\,136\,160\,576\,659$ | $0.109\,620\,474\,434\,489$ | Direct |  $0.001\,693\,276\,941\,446\,93$*
D |  D | $0.320\,741\,443\,721\,379$ | $0.111\,588\,574\,552\,381$ | Direct |  $0.004\,048\,965\,158\,580\,58$*
Table 4. Detailed results for fairness measure AUC Gap for each transfer
scheme evaluated. The final column gives the $p$-value of the hypothesis test
of $\textrm{AUC~{}Gap}\neq 0$ for the transfer scheme evaluated. $*$ indicates
we reject $H_{0}$ at $\alpha=0.05$.

###  D.2. Subgroup-Specific Transfer Detail

This section gives additional results regarding intersectional model
performance discussed in Section 6.2. Figure 4 provides the results of each
model transfer scenario (local, direct, voting, stacked), organized by
intersectional subgroups.

Figure 4. (a) Left: Model performance over intersectional subgroups for
various transfer schemes evaluated (Male, Female, URM, Non-URM) for all
institutions. (b) Right: $\Delta$AUC values over sensitive subgroups for
various transfer schemes evaluated. One-SE error bars shown for both figures.
Direct and local transfer models are in lexicographic order (A, B, C, D)
within each subgroup.

Figure 4 provides additional evidence regarding the zero-shot transfer
capacity of models learned via direct transfer and voting transfer: their
subgroup performance tends to be similar to the local model, with no
discernable effect on performance disparities, measured by AUC gap. Most
transfer schemes also have limited effect on subgroup performance relative to
the local model, measured by $\Delta\textrm{AUC}(\textrm{local},\cdot)$, as
shown in Figure 4b. The exception to this is the stacked transfer model, which
tends to have both improved performance relative to the local model (high
$\Delta\textrm{AUC}(\textrm{local},\textrm{stacked})$) and reduced disparities
between groups (low AUC gap; see Figure 3).

###  D.3. Non-Intersectional Comparison for Figure 3

In Section 6.2, we discuss the significance of analyzing model performance
disparities via intersectional groups. Here, we present evidence of the
difference between the intersectional and non-intersectional (which we refer
to as “marginal”) analysis.

Figure 5. Non-intersectional (“marginal”) version of Figure 3, where AUC is
computed over marginal groups, not intersectional groups. In comparison to
Figure 3, this analysis shows considerably smaller disparities. This
demonstrates how marginal analyses can mask intersectional performance
disparities.

Figure 5 shows an identical analysis as Figure 3, with the exception that
subgroup performance is computed over marginal (non-intersectional) subgroups.
Here, we can see that, for each subgroup, the performance of the model is a
weighted average of the previous intersectional groups, reducing the observed
performance disparities and masking larger disparities within the
intersectional groups.

###  D.4. Impact of Ensemble Selection Strategies

We provide results comparing the impact of different model selection
strategies in Figure 6.

Figure 6. Test AUC by ensemble type and selection rule.

###  D.5. Impact of Functional Form for Base and Stacked Ensemble Models

In this section, we provide additional results for LightGBM, MLP models not
discussed in the main text due to space limitations.

We provide identical experimental results as our figures in the main text
here, using LightGBM and MLP models in place of L2LR. Figure 7 shows results
analogous to main text Figure 1; Figure 8 shows results analogous to main text
Figure 2; and Figure 9 provides results analogous to Figure 3. The results
shown for LightGBM and MLP models are consistent with those discussed in the
main text.

(a) Overall results for LightGBM model.

(b) Overall results for MLP model.

Figure 7. Overall results for LightGBM (7(a)) and MLP (7(b)) models. The
findings are consistent with our findings for $L_{2}$-regularized logistic
regression shown in Figure 1.

(a) Results for LightGBM model.

(b) Results for MLP model.

Figure 8. Additional results for LightGBM (8(a)) and MLP (8(b)) models. The
findings are consistent with our findings for $L_{2}$-regularized logistic
regression shown in Figure 2: the 95% CI for AUC for voting transfer overlaps
with the local model, for all institutions and for both LightGBM and MLP.
Additionally, the 95% CI for $\Delta\textrm{AUC}$ overlaps with zero,
indicating no transfer gap between the voting transfer model and the local
model.

(a) Results for LightGBM model.

(b) Results for MLP model.

Figure 9. Additional results for LightGBM (9(a)) and MLP (9(b)) models. The
findings are consistent with our findings for $L_{2}$-regularized logistic
regression shown in Figure 3: the 95% CI for AUC Gap for voting transfer
overlaps with the local model, for all institutions and for both LightGBM and
MLP, indicating no difference in the intersectional subgroup performance
disparities between the voting transfer model and the local model.

###  D.6. Regularization Study

(a) Regularization study results for L2LR model.

(b) Regularization study results for LightGBM model.

(c) Regularization study results for MLP model.

Figure 10. Results of regularization study over various $L_{2}$ regularization
strengths for local and direct transfer models. Left: Test AUC (lines) and AUC
Gap (bars). ‘*’ marker indicates the value $\lambda^{*}$ which achieves
highest test AUC for the given model type and source/target institution.
Right: Intersectional subgroup model performance.

Prior work suggested that regularization affects model fairness by controlling
worst-group outcomes, including in modeling regimes relevant to our fairly
simple $L_{2}$-regularized logistic regression approach. For example,
(Kamishima et al., 2011) shows that a regularizer consisting of an $L_{2}$
penalty, combined with a “prejudice removal” regularizer, can reduce a measure
of unfairness. However, their specific formulation of unfairness seeks to
minimize the model’s reliance on sensitive attributes to avoid disparate
treatment, while in our experiments, we do not seek to explicitly avoid this.
Using distributionally-robust neural network training, (Sagawa et al., 2019)
showed that increasing regularization (via increasing an $L_{2}$ penalty or
via early stopping) improves worst-group accuracy. (Khani and Liang, 2020)
suggested that the removal of spurious (i.e. non-informative) features can
have disproportionate effects on subgroups. We are aware of no previous work
which explores the effect of regularization on cross-institutional transfer,
despite the clear connection between regularization, the bias-variance
tradeoff, and generalization error, which could have implications for domain
transfer.

In this section, we conduct an exploratory study of the impact of
regularization on overall performance, and on equitable performance over
intersectional subgroups. Our procedure is as follows: for each training
experiment above, we fix the $L_{2}$ regularization penalty parameter
$\lambda\in{0,10^{-4},10^{-3},\ldots,10^{4}}$ and follow the same training and
evaluation procedure. We only conduct this for local and direct transfer
scenarios. Our aim in this study is to determine how regularization might
affect transfer, and how specific subgroups are affected.

Results of this study are shown in Figure 10. First, the dotted lines in
Figure 10a indicate AUC at different levels of regularization, which shows the
standard expected result that (due to bias-variance tradeoff) regularization
tends to have an “optimal” value (indicated by a ‘*’ dot), above or below
which a model’s test performance tends to decline.

Figure 10b shows that each intersectional subgroup tends to respond similarly
to regularization, and that changes in regularization generally fail to reduce
performance disparities across all source-target institution pairs, with the
rank-ordering of model performance for subgroups largely consistent across
source institutions.

We discuss the results in further detail in Section 6.

Figure 11. Overall performance (measured by AUC) vs. fairness (AUC Gap, Eq.
(3)).

###  D.7. Model Similarity Analysis

While our experiments demonstrate that models trained locally at each
institution have similar average performance to each other, our experiments do
not verify that these models learn similar functions of the inputs; instead,
they merely verify that their average performance on each institution’s test
set is similar. In this section, we briefly explore whether the learned
coefficients are similar between local models learned at each institution.

A standard method to compare whether logistic regression coefficients differ
between two datasets requires multi-institutional training (having access to
all datasets), and would involve adding an institution indicator variable, and
determining whether the coefficient corresponding to this variable was nonzero
in the fitted model. However, since we are unable to train directly on multi-
institutional datasets due to the privacy constraints mentioned above, we
explore alternative methods for model comparison. These methods should be
considered qualitative explorations of the similarity of the learned models.

We provide two exploratory analyses to address this question. First, in Figure
12, we compute an overlap metric, $\textrm{Overlap}@k$, for the local models
from each pair of institutions. $\textrm{Overlap}@k$ is computed as follows:
let $\hat{\theta}=[\theta_{1},\ldots,\theta_{d}]$ represent the
$d$-dimensional coefficients of a model. For each pair of
$\hat{\theta}_{i},\hat{\theta}_{j}$, we separately sort the elements in
descending order by magnitude $sort(\hat{\theta})$. Then, for fixed $k$, we
take the first $k$ elements of both vectors and compute the size of the
overlap:

(4)
$\textrm{Overlap}@k(\hat{\theta}_{i},\hat{\theta}_{j})=\big{|}sort(\hat{\theta}_{i})[1:k]\cap
sort(\hat{\theta}_{j})[1:]\big{|}$

Intuitively, $\textrm{Overlap}@k$ measures the level of agreement between
models about which coefficients are largest in magnitude. This does not, for
example, ensure that these coefficients have even the same direction, but it
provides a qualitative measure of agreement on feature importance. Two models
which have identical rank-ordering of feature magnitudes would have
$\textrm{Overlap}@k$ of $k$, the highest possible value; two models which do
not agree on any of the highest-$k$-magnitude features would have
$\textrm{Overlap}@k$ of zero.

Because it can be easier to interpret the overlap as the relative size of the
intersection, we also report the Normalized $\textrm{Overlap}@k$, obtained by
normalizing by a factor of $1/k$:

(5)
$\textrm{Normalized~{}Overlap}@k(\hat{\theta}_{i},\hat{\theta}_{j})=\frac{1}{k}\big{|}sort(\hat{\theta}_{i})[1:k]\cap
sort(\hat{\theta}_{j})[1:]\big{|}$

(a) Model similarity metric $\textrm{Overlap@}k$ for each pair of local
models.

(b) Model similarity metric $\textrm{Normalized~{}Overlap@}k$ for each pair of
local models.

Figure 12. The proposed model similarity measures for each pair of locally-
learned models.

Results of our computation of these similarity metrics are shown in Figure 12.

As an additional check of model similarity, which (unlike
$\textrm{Overlap@}k$) accounts for the directionality of the feature vectors,
we also report the cosine similarity between each pair of model coefficients.
Cosine similarity is a measure of the angle between two vectors, irrespective
of their magnitudes, and is defined as:

(6)
$cossim(\hat{\theta}_{i},\hat{\theta}_{j})=\frac{\langle\hat{\theta}_{i},\hat{\theta}_{j}\rangle}{||\hat{\theta}_{i}||\hat{\theta}_{j}||}$

Institution | B | C | D
---|---|---|---
A | $0.464\,488\,93$ | $0.397\,752$ | $0.269\,866\,66$
B |  | $0.337\,032\,19$ | $0.222\,562\,4$
C |  |  | $0.171\,349\,66$
Table 5. Model similarity measure
$cos(\hat{\theta}(X_{i}),\hat{\theta}(X_{i^{\prime}})$.

Results of this comparison are shown in Table 5

##  Appendix E Computing Standard Errors of AUC

As discussed above, we compute standard errors for AUC estimates according to
the procedure described in (Hanley and McNeil, 1982; Fogarty et al., 2005),
which utilizes the equivalence between the Area Under the Receiver Operating
Characteristic Curve and the Wilcoxon Statistic.

Formally, let $n_{p}=\sum_{i=1}^{n}\mathbbm{1}(y_{i}=1)$ and
$n_{n}=\sum_{i=1}^{n}\mathbbm{1}(y_{i}=0)$ be defined as the number of
positive and negative examples in the dataset of interest, respectively.
Define $A^{\prime}$ as the AUC on the dataset. Then, let

(7) $\displaystyle D_{p}$
$\displaystyle\coloneqq(n_{p}-1)(\frac{A^{\prime}}{2-A^{\prime}}-A^{\prime
2})$ (8) $\displaystyle D_{n}$
$\displaystyle\coloneqq(n_{n}-1)(\frac{2A^{\prime 2}}{1+A^{\prime}}-A^{\prime
2})$

Then the standard error of $A^{\prime}$ can be computed as:

(9)
$SE(A^{\prime})=\sqrt{\frac{A^{\prime}(1-A^{\prime})+D_{p}+D_{n}}{n_{p}n_{n}}}$

For further details and proof, we defer the reader to (Hanley and McNeil,
1982).