# Embracing the black box: Heading towards foundation models for causal
discovery from time series data

Gideon Stein, Maha Shadaydeh, Joachim Denzler

###### Abstract

Causal discovery from time series data encompasses many existing solutions,
including those based on deep learning techniques. However, these methods
typically do not endorse one of the most prevalent paradigms in deep learning:
End-to-end learning. To address this gap, we explore what we call Causal
Pretraining. A methodology that aims to learn a direct mapping from
multivariate time series to the underlying causal graphs in a supervised
manner. Our empirical findings suggest that causal discovery in a supervised
manner is possible, assuming that the training and test time series samples
share most of their dynamics. More importantly, we found evidence that the
performance of Causal Pretraining can increase with data and model size, even
if the additional data do not share the same dynamics. Further, we provide
examples where causal discovery for real-world data with causally pretrained
neural networks is possible within limits. We argue that this hints at the
possibility of a foundation model for causal discovery.

## Introduction

Figure 1: Comparison between a general depiction of causal discovery methods
(left) and our Causal Pretraining methodology (right). Instead of inferring
causal graphs from data directly, Causal Pretraining produces neural networks
that can be deployed for inference directly.

The investigation of causal discovery from time series data encompasses many
existing solutions, including, of course, the integration of deep learning
techniques. Despite the widespread utilization of these techniques, many
methods do not endorse one of the most prevalent paradigms in deep learning:
End-to-end learning. This paradigm suggests that it is often beneficial to
only provide neural networks with raw input data instead of handcrafting
features. Additionally, making assumptions on how a particular task should be
solved can hinder performance (Bojarski et al. 2016), (Amodei et al. 2016),
(Glasmachers 2017). Contrary to that, neural networks are typically embedded
into well-established causal discovery frameworks such as Granger causality,
(Tank et al. 2018), (Ahmad, Shadaydeh, and Denzler 2022), (Teodora Trifunov,
Shadaydeh, and Denzler 2022), (Löwe et al. 2022) or score-based methods (Zheng
et al. 2018), (Ng et al. 2019). Through this, the solution space is naturally
restricted. To address this disparity, we explore what we call Causal
Pretraining, a methodology that aims at learning a direct mapping from
multivariate time series to causal graphs as depicted in Figure 1. We propose
to parameterize this mapping by a deep neural network and train it in a
supervised manner. In the training phase, we sample from a distribution of
synthetic time series with known corresponding causal graphs. Besides leaving
the solution space completely open, Causal Pretraining has another distinct
advantage over many other deep-learning approaches. Since it does not require
fitting any parameters during inference and natively allows for effective
parallel processing, it makes the analysis of large sets of time series
exceptionally efficient. While this idea is, to our surprise, largely
unexplored, we determined that substantial challenges are stabilizing training
and encouraging behavior beyond learning correlational patterns. Therefore, we
conducted experiments involving training multiple deep-learning architecture
archetypes with differing training techniques on increasingly more complex
synthetic datasets. We specifically evaluate the test performance for
synthetic data samples that mimic the training dynamics (in-distribution) and
synthetic data samples with slightly altered dynamics (out-of-distribution).
To demonstrate the applicability of our approach to real-world data, we also
test our approach on in-the-wild datasets with completely unknown data
distributions in a zero-shot setting.

While much work still lies ahead, we empirically show that Causal Pretraining
can consistently uncover causal relationships for unseen time series, assuming
that the training and test time series samples share most of their dynamics.
More importantly, we also find that the performance of Causal Pretraining
increases with model size and the amount of training data, even when the
additional training samples extend the data distribution. In these scenarios,
we show that Causal Pretraining can outperform alternative simple approaches
without fitting parameters for new data. We further find potential to truly
extrapolate to real-life data. We argue that this together hints at the
possibility of a foundation model for causal discovery. Finally, we emphasize
that this paper focuses on empirical results and the applicability of CP to
real-world data. We retain theoretical insights, e.g., identifiability
statements, for future work. In summary, we present the following
contributions:

  1. 1.

We explore supervised learning for causal discovery from time series data,
aiming at learning it end-to-end from synthetic data with shared dynamical
properties.

  2. 2.

We introduce and evaluate several helper techniques to support the performance
of Causal Pretraining.

  3. 3.

We evaluate the ability of causally pretrained neural networks to predict
real-world causal graphs.

  4. 4.

We observe relations to foundation models, as supported by our empirical
results.

## Background and Related Work

The discovery of causal relationships from observational time series can be
tackled in various ways (Gong et al. 2023), (Assaad, Devijver, and Gaussier
2022), (Vowels, Camgoz, and Bowden 2022), (Runge et al. 2023). Here, we give
an overview of these methods and elaborate on how they relate to causal
pretraining.

Score-based approaches aim to find a causal graph that maximizes a defined
scoring function (e.g., AIC score (Akaike 1992)). With the introduction of
formulating the scoring as a continuous optimization problem (Zheng et al.
2018), (Pamfil et al. 2020), the possibility of deploying neural networks
arose quickly. For causal discovery in data without temporal dimension (sample
data), a multitude of methods that deploy deep-learning architectures was
developed ((Lachapelle et al. 2020), (Ng et al. 2019),(Kyono, Zhang, and van
der Schaar 2020)). Concerning time series data, (Sun et al. 2023) adapts the
previously used vectorized autoregressive model (VAR) from (Pamfil et al.
2020) to handle nonlinear relationships by deploying a 1D convolution-based
architecture.

Being exclusively applicable to time-series data, Granger causality(Granger
1969) has a substantial history. At its core, it evaluates whether a certain
variable’s history helps with predicting another target variable. Deep
learning-based Granger causality methods mostly deploy neural networks as
forecasting architectures and infer Granger causality in various ways.
(Montalto et al. 2015) and its extension (Wang et al. 2018) deploy a greedy
search over which input variable to use with neural networks to determine
Granger-causes. (Tank et al. 2018) and (Tank et al. 2021) alternatively use
the weights of the first layer of an MLP under $L2$ regularization of the same
layer to determine Granger-causes. Other methods infer from attention weights
(Guo, Lin, and Antulov-Fantulin 2019), (Dang, Shah, and Zerfos 2018) or the
parametrization of variational autoencoders (Li, Yu, and Principe 2023), (Meng
2019). Furthermore, approaches such as (Ahmad, Shadaydeh, and Denzler 2022)
propose to generate in-distribution intervention variables and determine
Granger causes using the model invariance assumption. Importantly, in all
approaches mentioned so far, neural networks are optimized for a single
specific dataset.

Framing causal discovery as a supervised learning task was also explored to
some extent. Concerning sample data, an early work that does not deploy deep
learning is (Lopez-Paz et al. 2015), which aims at learning a binary
classifier to direct a link between two variables from data. Some recent
strain work that leverages deep learning methods to map from data correlation
matrix to directed acyclic graph is (Li, Xiao, and Tian 2020) and (Petersen et
al. 2023). (Geffner et al. 2022) aims at learning an autoregressive flow model
(Huang et al. 2018) from data that can be used for causal discovery. Finally,
as the work that is closest to our methodology, (Löwe et al. 2022) aims at
learning a mapping from multivariate time series to causal graph by deploying
a Variational autoencoder-based architecture to forecast the time series. The
encoder output is then leveraged to infer Granger-causes for each variable. On
the contrary, we aim to learn direct mappings without a surrogate task.
Another crucial disparity from (Löwe et al. 2022) is that we frame Causal
Pretraining to uncover the time lags of any causal relationship rather than
only returning a summary graph that ignores temporal patterns. To the best of
our knowledge, our proposed method is the first that aims to learn causal
discovery for time series completely end-to-end.

## Method

Figure 2: Depiction of architectures that we consider for Causal Pretraining.
From left to right: GRU, Transformer, ConvMixer, MLP. We further mark
locations for correlation injection with *.

Here, we formally introduce our methodology and discuss assumptions. We
subsequently detail the architectures and the data generation process we used
to test our approach. Finally, we suggest various training techniques and
assess their impact on Causal Pretraining.

### Definitions & Assumptions

We define $\mathbb{X}=(x^{t}_{i})_{i=1,..,V;t=0,..,T}$ to be a multivariate
time series with $V{\in\mathbb{N}^{+}}$ variables and a length of
$T{\in\mathbb{N}_{0}}$. We assume, for now, that any $x_{i}^{t}$ contained in
$\mathbb{X}$ can be described by the following time-invariant structural
equation model:

$x_{i}^{t}=\sum_{n=1}^{N}\sum_{j=1}^{V}f_{i,j}^{n}(\mathbb{A}^{i,j,n}\cdot
x^{t-n}_{j})+e^{t}_{i}~{}~{}~{}~{}.$ (1)

Here $\mathbb{A}$ is a three-dimensional tensor where element
$\mathbb{A}^{j,i,n}$ denotes a coefficient that describes the (causal) impact
of a specific variable $j$ at a specific time lag $n$, i.e., $x^{t-n}_{j}$, on
$x^{t}_{i}$. $N$ denotes the maximum time lag considered. Each linear effect
is then transformed by an individual function $f_{j,i}^{n}$ to account for
possible nonlinear relationships. Additionally, $(e^{t}_{i})_{i=1,..,V}$
denotes uncorrelated Gaussian noise.

Causal discovery methods (CDMs) are concerned with uncovering the set of non-
zero elements of $\mathbb{A}$ from a given time series $\mathbb{X}$. Typically
they either aim at uncovering a summary graph that is represented by an
adjacency matrix $G\in\mathbb{Z}^{V}\times V$ where element $(i,j)$ denotes
whether any current or past observation of variable $x_{j}$ has an impact on
variable $x^{i}$. Formulated differently, it specifies whether the parameter
vector $\mathbb{A}^{i,j}$ has any non-zero elements. Alternatively, methods
that aim at uncovering a window causal graph return a 3-dimensional tensor
$G\in\mathbb{Z}^{V\times V\times N}$ where element $(i,j,n)$ specifies whether
$\mathbb{A}^{i,j,n}$ is estimated to be non-zero. Based on this formalism, we
can naively summarize CDMs as: $\textrm{CDM}(\mathbb{X})\rightarrow G$.
Contrary to that, Causal Pretraining is not concerned with directly uncovering
any causal graph $G$, but rather with producing a causally pretrained neural
network (CPNN) in a supervised manner that can be applied in zero-shot
settings (no further parameter optimization) to infer $G$. We define
$\mathcal{G}$ as a set of structural equations (Equation 1) that each
specifies the causal dynamic of a multivariate time series. Additionally, we
define $\mathcal{X}$ to be a set of corresponding $\mathbb{X}$ that originates
from a specific element in $\mathcal{G}$. Formally, Causal Pretraining (CP)
can be defined as follows:

$\displaystyle\textrm{CP}(\mathcal{X},\mathcal{G})\mapsto\textrm{CPNN},\hskip
7.11317pt\textrm{CPNN}(\mathbb{X})\mapsto G\in\mathbb{Z}^{V\times V\times N},$
(2)

where CPNN refers to a causally pretrained neural network. We treat the
elements of the network output $G$ as probability estimates that the
corresponding elements in $\mathbb{A}$ exist. Throughout this paper, we make
the following assumptions: 1. $G$ is a Directed Acyclic Graph (DAG). No
instantaneous effects. 2. Causal sufficiency: All causes are observed. 3.
Theoretical insights such as (Shah and Peters 2020) suggest that learning a
CPNN that can correctly identify the non-zero elements of $\mathbb{A}$ for any
$\mathbb{X}$ is very likely impossible. Instead, we assume that train and test
distribution share general dynamics, such as the functional space $f$ in
Equation 1 from which we draw elements for all synthetic data samples.

### Architectures

To properly evaluate our methodology, we deem it essential to evaluate
multiple differing architectures. We, therefore, select five different
architectures, aiming at covering the prominent deep-learning archetypes up to
this date and not necessarily focusing on fully optimizing the architecture
for Causal Pretraining for now. We test an MLP (Taud and Mas 2018), a
unidirectional GRU (uGRU), a bidirectional GRU (bGRU), a Conv Mixer CM
(Trockman and Zico Kolter 2022), a recently introduced convolutional
architecture that showed strong results on image tasks, which we adapt for
time series and a Transformer (Trf) that borrows heavily from the Informer
(Zhou et al. 2021) architecture excluding sparse attention but featuring
Attention Distillation (Zhou et al. 2021). All architectures are depicted in
Figure 2 (both GRU architectures are jointly depicted). We keep input and
output dimensions for all architectures the same (input: $\mathbb{X}$, output:
causal graph $G$, optional: regression surrogate task as described below). All
networks return a vector with the length $V*V*N$ that we interpret as
probabilities for specific elements of $\mathbb{A}$ to be non-zero. We reshape
this vector into $G^{V\times V\times N}$ and then calculate binary cross-
entropy for the primary loss component with $\mathbb{A}>0$ as the label. To
make the comparison fair, we scale the architectures to have similar amounts
of parameters, aiming at estimating the innate capabilities of these
archetypes. In total, we deploy five sizes in our experiments (although not
all sizes during every experiment), which we denote as ”small” ($\sim$13k
params), ”medium” ($\sim$120k params), and ”big” ($\sim$1.5M params) ”deep”
($\sim$17M params), and ”lcm” (”large causal model”, $\sim$ 300M params),
seeAppendix 3.

### Additional Training Techniques

While deep learning architectures are, in theory, universal function
approximations (Hornik, Stinchcombe, and White 1989), in reality, learning a
proper function from observational data is not always straightforward.
Networks often converge to local minima or memorize data, which we attempt to
counter by employing the following three techniques to help with the
optimization process.

##### Regression Output

An easy-to-achieve suboptimal solution in our training setup is predicting all
elements of $\mathbb{A}$ as zero. This often results in a small loss given
that the true number of non-zero elements in $\mathbb{A}$ ($|\mathbb{A}>0|$)
is small. To discourage this solution, we add an optional regression output
that predicts the number of non-zero elements in $\mathbb{A}$. We formulate
the loss related to this prediction as follows:

$\textrm{regLoss}=(\hat{Y}_{reg}-|(\mathbb{A}>0)|)^{2}$ (3)

where $\hat{Y}_{reg}$ specifies the regression output. This task should be
trivial when the correct edges are identified (counting), and this penalty
term should be close to zero. However, predicting a graph with no edges leads
to a high penalty.

##### Correlation Regularization

Additionally, since no correlation typically implies no causation, we
introduce a regularization term called correlation regularization (CR). This
term punishes the case where a model is confident that a specific element of
$\mathbb{A}$ is non-zero (high confidence in the model output $G$), but the
lagged-crosscorrelation of the corresponding time series is low. CR is defined
in the following way:

$\displaystyle CR(G,\mathbb{X})$
$\displaystyle=\sum_{i=1}^{V}\sum_{j=1}^{V}\sum_{n=1}^{N}\left(\frac{G^{i,j,n}}{|\mathit{lcc}(\mathbb{X}_{i},\mathbb{X}_{j},n)|+\beta}\right)^{\alpha},$
(4) $\displaystyle\mathit{lcc}(a,b,n)$
$\displaystyle=\frac{\sum\limits_{t=0}^{T}(a^{t}-\bar{a})\cdot
L^{n}(b^{t}-\bar{b})}{\sqrt{\sum\limits_{t=0}^{T}(a^{t}-\bar{a})^{2}}\sqrt{\sum\limits_{t=0}^{T}\left(L^{n}(b^{t}-\bar{b})\right)^{2}}},$
(5)

where $L^{n}$ is the lag operator (shifting the time series $n$ steps).
Furthermore, $\alpha$ and $\beta$ are hyperparameters determining the exact
shape of the function. We include a depiction of CR in the Appendix 5.
Notable, the term does not reward high confidence for predictions with
corresponding high cross-correlation. Nor does it punish low confidence for
edges with corresponding high cross-correlation values. It thereby only
encodes the idea that no correlation implies no causation.

##### Correlation Injection

Many causal discovery methods take a skeleton graph that encodes correlations
between variables as a starting point for causal discovery ((Spirtes et al.
2000),(Li, Xiao, and Tian 2020),(Petersen et al. 2023)). To mimic this and to
help the learning process, we fuse (concatenate to the current hidden state)
the lagged cross-correlation of all time series in $\mathbb{X}$ into the
network as depicted in Figure 2.

### Data

#### Synthetic Data

To perform Causal Pretraining, we require a large set of training examples. As
real-world data with labels, i.e., ground-truth causal graphs, are typically
rare, we generate sets of synthetic data ($\mathcal{G},\mathcal{X}$) to train
on. We randomly select elements of $\mathbb{A}$ to be non-zero to create a
single training example. We then randomly sample all values of $\mathbb{A}$
that are non-zero from a specified uniform distribution and draw nonlinear
relations $f_{i,j}^{n}$ from a set of specified functions:{$e^{x}$, $x^{2}$,
$\sigma(x)$, $sin(x)$, $cos(x)$, $relu(x)$, $log(\sigma(x))$, $\frac{1}{x}$,
$\|x\|$, $clamp(x,(-0.5,0.5)$}. For linear datasets, we generate data from
vector autoregressive models, i.e., we set all $f^{n}_{i,j}(\cdot)=(\cdot)$ in
Equation 1. Then we generate $\mathbb{X}$ according to this dynamic. A
detailed description of this process is included in Appendix 1. Since there is
no guarantee that randomly sampled structural equations (Equation 1) lead to a
stable system, we establish stability tests to exclude unstable systems from
the datasets. Finally, we apply min-max normalization to the time series. We
refer to Table 4 (Appendix) for further specifications of the datasets that we
use for training. We also provide additional data information in the
Experiment section Experiments.

#### Kuramoto

A frequently used source for synthetic data is fully observable physical
simulations. Similar to (Löwe et al. 2022) from which we also adapt the
simulation, we perform Causal Pretraining on data originating from a Kuramoto
model (Kuramoto 1975) with five variables. Since we are primarily concerned
with one-dimensional variables, we use the trajectories of the simulated
variables as one-dimensional time series. Notably, the dynamics of this
dataset do not strictly follow Equation 1. We, therefore, empirically evaluate
with this dataset whether we can relax our initial assumption.

#### Zero-shot Inference

Another capability of Causal Pretraining we aim to explore in this work is
whether it can extrapolate to real-world data outside the training
distribution. To test this, we perform zero-shot inference on two distinct
benchmarks, meaning we do not perform any further parameter optimization for
unseen data. First, we predict the causal relationships in a benchmark
involving the discharge of rivers in Germany (Ahmad, Shadaydeh, and Denzler
2022). Secondly, we test the causal direction in a real-life dataset
originating from (Jesson et al. 2021), involving the estimation of aerosol-
cloud interactions. Since the dataset is originally concerned with estimating
the average treatment effect of aerosol on different cloud parameters under
weather confounding (meaning the direction of the effect is clear), we are
concerned with confirming this causal direction by only evaluating the
predicted direction between these two variables under the influence of other
weather variables (we consider sea surface temperature, effective inversion
strength, and relative humidity at 850 mb).

## Experiments

To properly evaluate Causal Pretraining, we conducted four studies aiming at
the step-by-step evaluation. During all experiments, we compare CPNNs with two
simple baseline techniques and one popular causal discovery method for time
series data (PCMCI, (Runge et al. 2019)). We additionally compare the results
on the Kuramoto data with results provided in (Löwe et al. 2022). For
baselines, we calculate the absolute lagged cross-correlation for all
variables and use them directly as probability estimates for $\mathbb{A}$. We
refer to this as Correlation Thresholding (CT). Additionally, we perform a
linear form of Granger-causality GVAR by fitting a VAR model to the data and
treating the absolute parameters of the model as probability estimates for
$\mathbb{A}$. Further, we deploy the PCMCI algorithm using partial correlation
as the conditional independence test.

|  | MLP | uGRU | bGRU | CM | Trf | CT | GVAR | PCMCI
---|---|---|---|---|---|---|---|---|---
|  | Causal Pretraining | Baselines
Test-Set 1
| SL | .999 (.000) | 1.00 (.000) | .999 (.000) | .999 (.000) | 1.00 (.000) | .997 | 1.00 | 1.00
| ML | .498 (.005) | .621 (.053) | .626 (.185) | .513 (.014) | .621 (.125) | .997 | 1.00 | 1.00
| SNL | .950 (.001) | .955 (.001) | .948 (.002) | .949 (.002) | .955 (.003) | .918 | .916 | .915
| MNL | .525 (.004) | .829 (.102) | .555 (.104) | .519 (.004) | .545 (.009) | .937 | .938 | .941
| LNL | .933 (.001) | .937 (.001) | .937 (.001) | .935 (.002) | .934 (.001) | .936 | .944 | .943
Single | XLNL | .499 (.006) | .689 (.111) | .749 (.138) | .506 (.004) | .518 (.034) | .938 | .944 | .943
| Medium | .928 (.023) | .907 (.023) | .920 (.012) | .887 (.003) | .950 (.015) |  |  |
Joint | Big | .761 (.028) | .959 (.028) | .962 (.032) | .886 (.003) | .977 (.001) | .958 | .888 | .946
Test-Set 2
| SL | .999 (.000) | 1.00 (.000) | .999 (.000) | .999 (.000) | 1.00 (.000) | .999 | .999 | .999
| ML | .499 (.003) | .600 (.052) | .613 (.181) | .506 (.007) | .601 (.119) | .999 | 1.00 | 1.00
| SNL | .930 (.001) | .935 (.000) | .933 (.001) | .931 (.002) | .935 (.002) | .926 | .928 | .924
| MNL | .520 (.006) | .785 (.088) | .547 (.090) | .518 (.005) | .538 (.010) | .927 | .927 | .927
| LNL | .905 (.002) | .915 (.002) | .916 (.001) | .912 (.002) | .916 (.001) | .910 | .912 | .905
Single | XLNL | .502 (.006) | .659 (.096) | .710 (.124) | .503 (.006) | .518 (.027) | .913 | .913 | .910
| Medium | .916 (.023) | .895 (.022) | .906 (.011) | .869 (.003) | .939 (.015) |  |  |
Joint | Big | .752 (.027) | .946 (.038) | .952 (.033) | .867 (.002) | .970 (.001) | .948 | .862 | .910
Table 1: Mean AUROC scores for the synthetic data experiments Single and Joint
(bottom two lines of each Test-set). For experiment Single, the first column
specifics the dataset, while for experiment Joint, it specifies model size.
Best results are denoted in bold. We report the corresponding standard
deviation calculated over 10 runs in brackets.

### Synthetic Data 1 - Impact of the Dataset

To evaluate the performance of CP, we conducted experiments on the precise
data distribution we described in the Data section Data. We continuously
evaluated two distinct test sets to understand extrapolation capabilities
during this synthetic data experiment. Firstly, a test set, named Test-Set 1,
includes test samples originating from the same distribution as the training
data. Secondly, a test set, named Test-Set 2, which has an increased variance
for the noise $e$ and an altered (slightly lower, not overlapping) range from
which we draw non-zero elements in $\mathbb{A}$ (see Equation 1). To stop
training, we perform early stopping based on the loss of an additional
validation set that follows the $\mathbb{A}$ range of Test-Set 2 but keeps the
training variance of the noise $e$. We use AdamW (Loshchilov and Hutter 2018)
as the optimizer during all experiments.

We trained all described architectures on six distinct datasets. Here, we
generated 5000 samples for training and 500 samples for testing, which have
different structural equations (Equation 1) with varying $\mathbb{A}$ and
differing $f$. We increased the complexity of the dataset step by step,
increasing the number of variables, the number of lags, the coefficient range,
and the set from which we draw the functions $f_{i,j}^{n}$. In short, we
tested two linear datasets (SL, ML), two nonlinear datasets with a reduced
nonlinear function set (SNL, MNL), and two datasets with the full function
set, as described in the Data section Data,(LNL, XLNL). In all three cases, we
considered three variables, a maximum lag of two, and the model size ”small”
for the first dataset. For the second dataset, we considered five variables, a
maximum lag of three, and the model size ”medium”. To compare the performance
of our method, we report the best-performing hyperparameter combination of
each architecture. We searched the optimal parameters of batch size, learning
rate, weight decay, and training addition (Regression Loss, CR, Correlation
injection) by performing a full grid search and ran each hyperparameter
combination twice. We then selected the combination that resulted in the
lowest observed validation loss and rerun it ten times.

Since we were also interested in the performance of CP when trained on data
that origins from different distributions, we conducted a second set of
experiments where we doubled the size of the six training sets that we
described above and joined them together, making the maximum number of lags
and the number of variables flexible. By this, we also mixed linear and non-
linear samples, effectively drawing from different data distributions. We
performed a similar hyperparameter search as in our first experiment. To keep
the search space reasonable, we omitted the regression head. We also always
included correlation injection since these hyperparameter selections performed
consistently better in our first synthetic data experiment. We independently
trained model sizes ’medium’ and ’big’ and rerun the best-scoring
hyperparameter combination ten times. We report the results of these studies
in Table 1. We denote the results of the first study with Single and the
results of the second study with Joint.

Surprisingly, we found that CP generally performed worse than our baselines in
our first set of experiments. With some exceptions, the AUROC scores on both
test sets were typically worse, even considering the best possible runs we
performed. From our architectures, uGRU and Trf seemed to perform slightly
better. However, these tendencies were too inconsistent to conclude a clear
trend. Contrary to that, the performance of CP in our second experiment set
outperformed all baselines, notably, while fitting no parameters on the test
sets. Since CDNNs have to learn a much more extensive training distribution to
perform comparably, we expected CDNNs to be less precise. We found the
opposite to be true. Even if we kept the architecture size the same, e.g.,
’medium’, we observed that the performance of CDNNs increased. Furthermore,
increasing the model size improved the performance and, most importantly, the
generalization (Test-Set 2). We interpret this in the following way: The
broader the training distribution, the more robust/generally applicable CPNNs
must become to solve the training distribution. This, in turn, helps with out-
of-training performance and generalization. Further, the amount of samples
required to optimize CP properly is much larger than we initially expected. We
suggest that further improvements could be achieved by making the training
distribution even broader, even for similarly sized architectures.

### Synthetic Data 2 - Impact of Model Size

Figure 3: Relationship between the Model size and the performance on datasets with an increased number of variables. We display the performance on Test-set 2 for each data point. | ACD* | MLP | uGRU | bGRU | CM | Trf | CT | GVAR | PCMCI
---|---|---|---|---|---|---|---|---|---
Test-Set
Kuramoto | .952 | .825 (.025) | .905 (.053) | .852 (.076) | .954 (.010) | .888 (.070) | 0.628 | 0.464 | 0.523
Rivers |  | 0.425 | 1.00 | 0.5000 | 0.600 | 1.000 | 1.00 | 1.00 | 1.00
Aerosol-Cloud |  | 0.00 | 0.017 | 0.793 | 1.00 | 0.150 | 0.473 | 1.00 | 0.363
Table 2: We here report mean AUROC scores for the Kuramoto dataset, AUROC
scores for the highest scoring CPNNs on the River benchmarks, and Accuracy for
the Aerosol-Cloud benchmark. The highest scores are denoted in bold. We
additionally report the variance, calculated over 10 runs on the Kuramoto
dataset.in brackets. * (Löwe et al. 2022).

As we investigated the relationship between the training distribution and the
performance of CP, we also wanted to explore the relationship between the
number of parameters and the ability to learn increasingly more complex
datasets. For this, we generated three synthetic linear datasets and stepwise
increased the number of variables to 10. We performed Causal Pretraining on
each dataset, trained varying model sizes independently, and performed the
exact hyperparameter search as in the previous chapter. We selected the
performance of the best-scoring hyperparameter combination of the best-
performing architecture. We then retrained this configuration five times to
calculate the final reference scores reported in Figure 4. Note that for the
size ”lcm” we restricted our search to the Trf and the CM architecture. We
find that the parameter count of the model determines the ability to perform
causal discovery properly. Specifically, there seems to be a parameter
threshold under which no proper solution can be learned (AUROC 0.5). We also
find that the extrapolation capabilities increase even when keeping the same
number of data samples (contrary to what one would typically expect concerning
overfitting). Further, the required model size for certain variables was much
bigger than expected. However, we suggest that this might be partly because
discovering a causal graph $G$ with multiple lags requires the estimation of
$V\times V\times N$ values, which might be hard for CPNNs. This suggests that
reducing the number of lags might reduce the required parameters in the
future. Together, we conclude from this that to improve the performance of CP,
we need to increase its scaling, especially considering that it is likely that
learning much broader distributions will also require an even higher parameter
count.

### Kuramoto

To bridge the gap to (Löwe et al. 2022), we evaluate CP on data from a
Kuramoto Model with five variables. We generated 50,000 samples for training
and 5,000 samples for testing, originating from a simulation of this model.
Further, we kept the same simulation settings as in (Löwe et al. 2022) and
ignored the diagonal of $G$ (autoregressive links) to make our experiments
directly comparable. We again performed a hyperparameter search for each
architecture and retrained the best hyperparameter combination ten times to
report the standard deviation. We report the results of these experiments in
Table 2. Here, the CM architectures performed best and achieved similar, if
not slightly better, results than (Löwe et al. 2022). Further, all of our
baselines are decisively outperformed on this dataset, which we attribute to
the fact that the Kuramoto dataset does not follow Equation 1, which hinders
methods that rely on linear relationships.

### Zero-shot Inference

To test the performance of CPNNs when applied to truly out-of-distribution
data, we reuse the CDNNs from Synthetic Data 1 Synthetic Data 1 - Impact of
the Dataset on two benchmarks involving the discharge of rivers in Germany
(Ahmad, Shadaydeh, and Denzler 2022) and aerosol-cloud interactions (Jesson et
al. 2021). Since all of these datasets only specify a summary graph $G$, we
took the causal link of the first time lag as the prediction for the summary
graph. We report the results of this experiment in Table 2. Importantly, since
we wanted to perform this experiment as close to a real application of CPNNs
as possible, we do not report STD but inferred the summary graph once for each
sample from the full-time series and with the highest-scoring models from
Synthetic Data 1 Synthetic Data 1 - Impact of the Dataset.

We found that the performance of CPNNs on unseen data distribution differs
widely between model architectures and datasets. While the river benchmark is
properly predicted by the uGRU and the Trf architecture, these architectures
are specifically outperformed by CM on the aerosol dataset. As a side note,
(Ahmad, Shadaydeh, and Denzler 2022) or originally (Gerhardus and Runge 2020)
suggest that the river benchmark is more challenging than our scoring
suggests. This is, since they report results for fixed p-values, which is not
required when calculating AUROC scores. While the performance of CP is
improvable, we find it promising that models not trained on these datasets do
not break down entirely but display some extrapolation capabilities. We
believe this signifies that CPNNs incorporate some form of Causal Discovery
test that can uncover correct causal structures in more general settings than
the training distribution.

## Discussion and Conclusion

This work introduced Causal Pretraining, a methodology for supervised deep
end-to-end causal discovery from time series data. We conducted the first
experiments, providing evidence that our causally pre-trained neural networks
(CDNNs) can achieve similar results to other causal discovery methods without
fine-tuning any parameters during inference and being highly computationally
parallelizable. We provided evidence that CDNNs show some potential to
extrapolate to unseen real-life data outside of the training distribution.
Specifically interesting, the performance of CDNNs and its capability to
generalize increases with data complexity and model size. Under the assumption
that this trend continues beyond the scope of our experiments, we take this as
evidence that foundation causal models trained through Causal Pretraining are
possible. Recent developments in deep learning (OpenAI 2023) suggest that
consistent generalization by scaling up through data and model dimensions is
indeed possible. This idea also aligns with theoretical research such as
(Bubeck and Sellke 2021), (Bartlett et al. 2020) or (Brutzkus and Globerson
2019), suggesting that greatly over-parametrizing neural networks can help
with generalization. While we excluded these experiments in this paper since
they are probably intuitive for deep-learning practitioners, we also found
that both scalings must go hand-in-hand while performing Causal Pretraining.
Simply scaling up the architectures without increasing the dataset’s
complexity makes it arbitrarily easy for neural networks to remember the
training dataset and not generalize at all. Further, keeping the network too
small while increasing the data complexity in might make the learning task
impossible and, with that, also prevent generalization. We reserve keeping
this delicate balance while scaling up our methodology concerning data
distribution and model size for future research.

## Acknowledgments

We gratefully recognize the support of iDiv1, which is funded by the German
Research Foundation (DFG – FZT 118, 202548816). Special thanks from Gideon
Stein to Yuanyuan Huang1, Anne Ebeling1, and Nico Eisenhauer1 for supporting
me in this project and giving me the freedom to be creative with my research
ideas. Special thanks also to Christian Reimers 2 for the creative and helpful
exchange of ideas.

Gideon Stein is funded by the iDiv flexpool (No 06203674-22). Maha Shadaydeh
is funded by the Carl Zeiss Foundation within the scope of the program line
“Breakthroughs: Exploring Intelligent Systems” for “Digitization—explore the
basics (No P2017-01-003), use applications”.

1German Centre of Integrative Biodiversity Research 2Max Planck Institute for
Biogeochemistry Jena

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## Appendix

Here, we include additional specifications for the exact parameter counts for
all used architectures and sizes in Table 3 and data that we use throughout
this paper in Algorithm 1 and Table 4. Next, we include a study on inference
speed in Inference Speed Inference Speed and a depiction of Correlation
Regularization in Figure 5. While we expected that the importance of
hyperparameter selection would decrease with model size, we found no
consistent pattern in our experiments. To depict this, we display an example
of performance distribution over hyperparameter in Figure 6. Further, in
Preliminary studies Preliminary Studies: Architecture Capabilities, we
describe two small experiments on the baseline capabilities of our
architectures, which were historically performed before experiments in the
Experiment section Experiments. In Probabilistic studies Probabilistic
Predictions, we introduce a procedure that allows CPNNs to predict probability
distributions instead of probability scalars that might be useful for certain
applications. Finally, we provide a summary of all abbreviations used
throughout the paper in Table 5.

Algorithm 1 An algorithm with caption

: $maximum\char 95\relax lags(n),number\char 95\relax of\char 95\relax
variables(v)$

: $link\char 95\relax threshold,link\char 95\relax distribution$

: $ts\char 95\relax length,noise\char 95\relax var,number\char 95\relax
of\char 95\relax samples$

: $nl\\_selection$, $nl\\_threshold$

: $data\char 95\relax test(),graph\char 95\relax test()$

$\mathcal{X}=\\{\\}$

$\mathcal{G}=\\{\\}$

while $len(\mathcal{G})<number\char 95\relax of\char 95\relax samples$ do

$Draw:U(0,1)^{V\times V\times N}$

$PA:1\;\textbf{if}\;Draw>link\char 95\relax threshold\;\textbf{else}\;0$

$\mathbb{A}=U(link\\_distribution)\;\textbf{if}\;PA\;\textbf{else}\;0$

if nonlinear then

$Draw:U(0,1)^{V\times V\times N}$

$PA:1\;\textbf{if}\;Draw>nl\\_threshold\;\textbf{else}\;0$

$f:U(nl\\_selection)\;\textbf{if}\;PA\;\textbf{else}\;1$

else

$f:1$

end if

$\mathbb{X}=\\{\\}$

while $len(\mathbb{X})<ts\\_length$ do

generate $x^{new}_{i}$ according to Equation 1 $(\mathbb{A},f)$

end while

if $data\char 95\relax test(\mathbb{X})$ then

$\mathcal{X}\leftarrow X$

$\mathcal{G}\leftarrow G$

end if

end while

Size | Small | Medium | Big | Deep | LCM
---|---|---|---|---|---
MLP | 13.4k | 118k | 1.5M | 17.3M | -
uGRU | 13.0k | 126k | 1.6M | 17.2M | -
bGRU | 12.7k | 116k | 1.5M | 18.4M | -
CM | 13.3k | 128k | 1.4M | 17M | 286M
Trf | 12.3k | 120k | 1.4M | 16.1M | 391M
Table 3: Excact parameter count for all architectures and sizes we use
throughout this paper.

### Inference Speed

Since inference with CPNNs is highly parallelizable (batching), which we
denote as a neat advantage of CPNNs, we provide some short comparisons on
inference speed. For this, we reuse the dataset of the above section and
measure the speed to predict the corresponding test set with 500 samples each.
We perform inference on an Intel i7-7700 CPU, omitting GPU support from which
CPNNs would additionally benefit. We summarize the relationship between the
number of variables and the inference speed as follows: While our simple
benchmark techniques are still slightly faster since they come with closed-
form solutions for their optimization (and we additionally implemented a
batched version for CT), the inference speed of Causal Pretraining lies in the
same order of magnitude for all number of variables tested. In contrast, PCMCI
scales quadratically in our experiments. The number of conditional
independence tests that must be performed grows quadratically with the number
of variables, making it infeasible to infer from a large set of variables.
Importantly, all our methods (including PCMCI) are very fast to compute in
comparison to other approaches such as, e.g., (Tank et al. 2018) or (Ahmad,
Shadaydeh, and Denzler 2022), which require fitting neural networks for each
sample. We believe this feature of CPNNs makes it specifically beneficial in
areas where many similar samples have to be processed, such as in Earth and
neuroscience. Especially considering that they can outperform similarly fast
benchmarks.

Figure 4: Comparison of inference speed. Here, we use the architecture with the highest AUROC score for each dataset to represent CPNNs. We report the speed of computing the solution for 500 samples and 100 repetitions. Name | Pre | SL | ML | SNL | MNL | LNL | XLNL | Wide
---|---|---|---|---|---|---|---|---
Function set | L | L | L | NL1 | NL1 | NL2 | NL2 | NL2
Variables | 3 | 3 | 5 | 3 | 5 | 3 | 5 | 7/10/15
Maximum lag | 2 | 2 | 3 | 2 | 3 | 2 | 3 | 3
Coefficients (train) | br | br |  $\pm$ br | br |  $\pm$ br | br |  $\pm$ br |  $\pm$ br
Noise var (train) | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4
Coefficients (test 1) | br | br |  $\pm$ br | br |  $\pm$ br | br |  $\pm$ br |  $\pm$ br
Noise var (test 1 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4 | 0.4
Coefficients (test 2) | sr | sr |  $\pm$ sr | sr |  $\pm$ sr | sr |  $\pm$ sr |  $\pm$ sr
Noise var (test 2) | 0.6 | 0.6 | 0.6 | 0.6 | 0.6 | 0.6 | 0.6 | 0.6
Average non-zero | 9 | 2.7 | 7.5 | 2.7 | 7.5 | 2.7 | 7.5 | 14.7/30/67.5
Table 4: Dataset specifications. L denotes linear, NL1 denotes drawing only
from ($e^{x}$, $x^{2}$), and NL2 denotes the full function set specified in
the method Method section Method. Furthermore, sr denotes the range (0.2-0.3),
and br denotes the range (0.3-0.5). $\pm$ denotes that values drawn from a
range can be positive or negative. Wide specifies the datasets that were used
during Synthetic Data 2 Synthetic Data 1 - Impact of the Dataset. Pre
specifies the dataset used during Preliminary studies Preliminary Studies:
Architecture Capabilities.

### Preliminary Studies: Architecture Capabilities

Initially, we conducted two experiments to estimate our architecture’s general
capabilities. We used the model size ”small” for these three experiments and
chose a learning rate of 0.0001, a weight decay of 0.01, and a batch size of
64, performing no hyperparameter search.

First, we tested whether our architectures can correctly distinguish between a
linear and a nonlinear $\mathbb{X}$, which we deemed to be an essential
capability. For this purpose, we fixed which elements of $\mathbb{A}$ are non-
zero and only alter their actual values. We then added a nonlinear
$f^{n}_{j,i}$ for half of the samples as described in Algorithm 1. We
temporarily re-purposed the regression head by adding a Sigmoid function. We
treated the output as a binary classification and used binary cross entropy as
the loss function.

We found that the uGRU and the Trf architecture outperform the other
approaches in this limited setting (Increased AUROC scores on Test data),
framing them as the most promising candidates. While we found this to be
rather intuitive, since these are archetypes frequently applied to time
series, we also later found out that this advantage does not necessarily
translate into more general setups. We conclude that this supports our
approach of considering multiple architectures.

Second, we tested whether CPNNs can uncover the precise values in
$\mathbb{A}$. We again fix which values of $\mathbb{A}$ are non-zero and alter
only its coefficients. To train, we remove the sigmoid activation from our
output vector and treat it as a direct prediction for $\mathbb{A}$. We take
the original $\mathbb{A}$ as labels and optimize an MSE loss.

We found that none of our architectures can uncover the exact $\mathbb{A}$.
They instead converge on predicting the mean of each element in $\mathbb{A}$.
This behavior is consistent over all tested architectures, and we observed no
change even when weighing the loss values of non-zero elements higher than
those elements that are zero. We took this as a reason for our binary problem
formulation, aiming only at uncovering which elements are non-zero but not the
exact strength of the relationship. While we are confident that this behavior
might be altered with more sophisticated loss schemes or larger model sizes,
we keep this additional complexity for future research. Importantly, making
binary decisions aligns with many other causal inference methods.

### Probabilistic Predictions

Here, we tested whether we can adapt our method to produce distribution as
outputs instead of a single probability. We do this by running many short
samples of the same time series through a model and constructing a
distribution over output probabilities for each edge. It might be interesting
to analyze the form of these distributions in the future, which could help
detect wrongly classified edges or determine the exact decision threshold. As
an example of this procedure, Figure 6 holds the output distributions of a
uGRU model with the size ”big” for a single sample from the XLnL dataset.
Notably, some links have very high consistent confidence, while the prediction
varies much more for others.

Figure 5: Visualization of CR for $\alpha$ = 1.5 and $\beta$ = 0.15. The penalty is only big when the confidence is high while the correlation coefficient is low.  Figure 6: Left: Impact of hyperparameter selection. We report the standard deviation of the AUROC score on the validation set. For the synthetic data, we provide the joint dataset grid search results for model sizes ”medium” and ”big” and the grid search results for the dataset LnL for model size ”small,” ignoring all combinations that were not evaluated for the joint dataset. Right: Distributions over output probabilities for every edge in a single sample, sampled as described in Probabilistic studies Probabilistic Predictions. Colorful distributions denote true edges. Abbreviation | Full Name | Type
---|---|---
CP | Causal Pretraining | Method
CPNN | Causally Pretrained Neural Network | Method
MLP | Multi-Layer Perceptron | Architecture
uGRU | unidirectional Gated Recurrent Unit | Architecture
bGRU | bidirectional Gated Recurrent Unit | Architecture
CM | ConvMixer | Architecture
Trf | Transformer | Architecture
SL | Small Linear | Dataset
ML | Medium Linear | Dataset
SNL | Small Nonlinear | Dataset
MNL | Medium Nonlinear | Dataset
LNL | Large Nonlinear | Dataset
XLNL | Extra Large Nonlinear | Dataset
CP | Correlation Thresholding | Baseline
GVAR | Granger Causal Vectorized Autoregression | Baseline
LCM | Large Causal Model | Model size
CR | Correlation Regularization | Technique
Table 5: Summary of abbreviations used throughout this paper.


# Risk or Chance? Large Language Models and Reproducibility in Human-Computer
Interaction Research

Thomas Kosch  HU BerlinBerlinGermany<EMAIL_ADDRESS>and  Sebastian
Feger  Rosenheim Technical University of Applied SciencesRosenheimGermany
<EMAIL_ADDRESS>
###### Abstract.

Reproducibility is a major concern across scientific fields. Human-Computer
Interaction (HCI), in particular, is subject to diverse reproducibility
challenges due to the wide range of research methodologies employed. In this
article, we explore how the increasing adoption of Large Language Models
(LLMs) across all user experience (UX) design and research activities impacts
reproducibility in HCI. In particular, we review upcoming reproducibility
challenges through the lenses of analogies from past to future (mis)practices
like p-hacking and prompt-hacking, general bias, support in data analysis,
documentation and education requirements, and possible pressure on the
community. We discuss the risks and chances for each of these lenses with the
expectation that a more comprehensive discussion will help shape best
practices and contribute to valid and reproducible practices around using LLMs
in HCI research.

Large Language Models, Reproducibility, HCI Research, Research Methods

††ccs: Human-centered computing Human computer interaction (HCI)

##  1\. Introduction

Large Language Models (LLMs) impact and transform most areas of daily life,
from education and gaming to creativity and work. Exemplary LLMs are Llama,
Alpaca, or GPT-4, with the latter being made accessible to the general public
through OpenAI’s ChatGPT. Consequently, ChatGPT reached 1 million users within
five days after its release and currently has over 180 million
users111https://explodingtopics.com/blog/chatgpt-users. In light of the fast-
paced developments over the past few years and today’s adoption of LLMs across
large parts of society, LLMs have also become of great research interest. With
the rapid development in natural language processing and today’s great
accessibility of LLMs to the public, they are anticipated to become a
commonplace tool for data analysis in Human-Computer Interaction (HCI)
research. For example, LLMs have been explored to accelerate or support the
analysis of textual data in HCI (Tabone and de Winter, 2023), support the
user-centered design (UCD) process (Schmidt et al., 2024), simulate human
samples or replicate user studies (Aher et al., 2023), with the latter
practices being scrutinized by recent research (Agnew et al., 2024). As with
most significant scientific developments, today’s high research transparency
and validity standards demand a systematic understanding of how the use of
LLMs impacts reproducibility. Reproducibility is a major concern across
scientific fields. HCI, in particular, is subject to diverse reproducibility
challenges due to the wide range of research methodologies employed. The
broader scientific community has initiated complex discussions on the
potential impact of machine learning and Artificial Intelligence (AI) on
reproducibility (Ball, 2023; Gibney, 2022). We aim to contribute to this
discourse by focusing specifically on the research and adoption practices of
LLMs in the HCI community. This aligns with previous work that advocates for
the unique role and responsibility of HCI and human subject research in
promoting reproducible practices. Our goal is to design processes and tools
that foster scientific reproducibility, thereby enhancing the credibility and
validity of HCI research.

In this article, we explore how the increasing adoption of LLMs across all
user experience (UX) design and research activities impacts reproducibility in
HCI. In particular, we review upcoming reproducibility challenges through the
lenses of analogies from past to future (mis)practices, including p- and
prompt-hacking, general bias, support in data analysis, documentation, and
education requirements, and potential accelerated publication pressure on the
community. We discuss the risks and chances for each of these lenses with the
expectation that a resulting broader discussion will help shape best practices
and contribute to valid and reproducible practices around using LLMs in HCI
research.

##  2\. Large Language Models as Research Tool

LLMs are built using neural networks, which are computational models inspired
by the structure and function of the human brain, using the transformer
architecture as a key component. These models are trained on vast amounts of
text data, including books, articles, websites, and other written sources.
This data teaches the model about language patterns, syntax, semantics, and
other linguistic features. The text data is tokenized, broken down into
smaller units such as words, subwords, or characters presented numerically,
capturing semantic relationships between tokens. In a pre-training phase, the
transformer analyzes the tokens at once to decrease a loss function. After
pre-training, the model can be fine-tuned on specific tasks or domains to
improve performance. Once trained and tuned, the model can be used for various
tasks such as text generation, classification, or language translation. Yet,
the architecture of LLMs challenges the reproducibility of their outputs. Most
LLMs, including GPT-3.5 or GPT-4, are autoregressive models, generating each
subsequent token based on preceding tokens within the same sequence. Thus,
LLMs cannot holistically self-adjust or validate their outputs. Due to this
architectural limitation, LLMs show reduced reasoning and cannot utilize human
resources during generation to improve the precision or validation of the
output. Although users can use prompt engineering techniques to elicit more
thoughtful responses by either integrating specific phrasings within a prompt
or conversing over multiple messages with LLMs, these techniques increase the
likeliness of unequal outputs when repeating the process. We explain the
implications of these limitations in the following.

###  2.1. Value Lock-In

These characteristics complicate the reproducibility of outputs. LLMs are
prone to so-called “value lock-ins,” meaning that LLMs construct their
understanding of human behavior and decision-making by analyzing the norms and
attitudes found in human-written texts, such as those found on the internet
and in books. However, LLMs usually undergo training only once, missing
changes in user standing and opinions that can happen in the future. As a
result, the responses they produce may continue to reflect attitudes and
beliefs from the time of their initial training. The implications generate
research results that appear meaningful, although they may not reflect the
facts and beliefs of participants. For example, text-based analyses that
comprise interviews or think-aloud data are prone to this. Furthermore, this
is impeded by updating the used LLM, where the results can change between
versions. While specific parameters, such as the temperature function as
magnitude for output “randomness,” can be recorded, the exchange of whole
models may impact the research results unpredictably. Providing access to
previous LLMs, for example, through a repository outlining the LLM version,
used parameters, prompts, and outputs, may circumvent some of the described
issues.

###  2.2. Training Bias

LLMs are limited to knowledge that is represented in their dataset. ChatGPT,
for example, was trained on data available on the internet. Consequently, LLMs
are implicitly designed by a fraction of users who share similar properties:
persons with access to participate, design, and publish on the internet. LLMs
may reflect the views from Western, educated, industrialized, affluent, and
democratic backgrounds, reinforcing cultural bias and generating stereotypical
representations of marginalized populations when used to analyze research
data. Human reviewers can act as secondary observers to investigate the
outputs for biases. However, this approach is prone to confirmation biases,
where humans seek out, understand, prefer, and remember information that
aligns with or reinforces one’s existing beliefs or values. Depending on a
reviewer’s background, this may amplify the bias in LLMs through further
confirmation.

###  2.3. Hallucination

Hallucinations have challenged LLMs since their adoption by the public. LLM-
based text generation is susceptible to producing unintended content, leading
to a decline in the quality of the results. If the results are factually not
cross-evaluated with human experimenters, hallucinated results may not be
noticed at all and become published. Hallucinations are of great concern when
using LLMs to support or simulate human participation processes (Agnew et al.,
2024). For example, a lawyer tasked a language model with serving as a legal
assistant, resulting in a court filing filled with fictitious legal
references. This occurred partly due to the lawyer’s trust regarding the
authenticity of the referenced cases, which could be revealed through factual
testing. How would qualitative and quantitative analysis results be tested in
the context of HCI research? The HCI research community must validate methods
that test for hallucinations in HCI research results.

##  3\. Implications for Reproducibility in HCI Research

HCI research is characterized by a methodological diversity in designing and
evaluating systems that pose various reproducibility challenges already today
(Feger et al., 2019; Wacharamanotham et al., 2020). The expected widespread
adoption of LLMs as part of ideation support (Shaer et al., 2024), the
substitution of human participants for design requirement mapping and system
evaluations (Agnew et al., 2024; Schmidt et al., 2024), and as support for
data analysis (Tabone and de Winter, 2023) open up an entirely new spectrum of
reproducibility challenges in HCI research. We map risks and chances for HCI
reproducibility and discuss initial recommendations across these different
phases of UX research.

###  3.1. Learning from Today’s Reproducibility Challenges: Let’s not Repeat
Mistakes

Numerous factors contribute to the reproducibility challenges we face today.
In quantitative research, one major issue relates to p-hacking. P-hacking
refers to the selective reporting of statistical tests to achieve
statistically significant results, leading to inflated false positives and
compromised reproducibility. This practice not only undermines the integrity
of scientific research but also perpetuates a cycle of erroneous findings.
While moving towards the increasing adoption of LLMs in HCI research, we have
to consider how to address existing reproducibility challenges and carefully
navigate new pitfalls that might arise from LLMs. Analogous to p-hacking,
using LLMs during UX research is vulnerable to the so-called “prompt hacking.”
Prompt hacking of LLMs mirrors p-hacking in research by manipulating inputs to
influence outputs. As p-hacking selectively reports statistical tests to
achieve desired results, prompt hacking skews LLM responses by adjusting input
prompts. Both practices compromise integrity: p-hacking distorts scientific
findings while prompt hacking biases language model outputs. Recognizing these
parallels highlights the importance of transparency and integrity in research
and AI development, urging us to prioritize robust methodologies to uphold
credibility and reliability. Yet, the community can learn from the past to
avoid similar mistakes with new technologies in the future. We propose the
following to avoid repeating mistakes:

  1. (1)

We argue that adopting LLMs as part of UX research must consider
reproducibility challenges and specifically identify analogous issues
introduced by LLMs.

  2. (2)

We suggest learning from current best practices and advocating their adoption
for the use of LLMs. Regarding the examples of p-hacking and prompt-hacking,
we note that the applicability of established tools like pre-registration and
transparent, prompt protocols as part of manuscript submissions and paper
publications should be evaluated.

###  3.2. Bias Across User Experience Research

UX research and system evaluation fundamentally require knowledge about human
perception and experience. In this regard, HCI research today faces the issue
of bias through sampling experiences of too few or a biased set of human
samples. In this context, Schmidt et al. (Schmidt et al., 2024) stressed that
the “basic idea is that LLMs encode human experiences, which may be drawn upon
in design.” Expanding on this notion, we perceive a substantial opportunity
for LLMs to increase information’s robustness and consequent reproducibility
throughout the UX research process, from requirements mapping to system
evaluation. However, this approach also represents reproducibility risks.
Today, HCI research is confronted with the criticism that findings often
reflect the perspectives of young, educated, and Western communities. LLMs can
further aggravate this problem if they are sampled on reports and experiences
from a distinct part of society. Many experiences will reflect technology-
savvy individuals with a tendency for a younger population. Further, LLMs are
likely to favor specific languages and cultures. Any transparency regarding
these training biases further makes assessment of risks difficult. Concerning
bias and its impact on research reproducibility, we map multiple requirements:

  1. (1)

HCI should support the development of LLMs to make the selection of training
data and subsequent biases transparent.

  2. (2)

The HCI community should use multiple LLMs across UX research to reflect broad
human perspectives wherever necessary. Combining LLMs that lean towards
different regions or cultures is an example.

  3. (3)

Research and reviewers must critically examine the interconnections between
LLM training transparency, combinations of different LLMs, interplay with
additional direct human subject reporting, and the resulting deviation for the
specific activity and use case.

###  3.3. LLMs for Cross-Validation and Analysis Support

HCI is subject to a rich diversity of research methods unmatched in most other
fields. While we appreciate this richness, it comes with various
reproducibility issues subject to specific methods, which generally impact HCI
research reproducibility. Many HCI researchers are involved in activities
across multiple methodologies. As it is difficult to gain the same expertise
across all methods, individual researchers might find it more challenging to
evaluate and counteract reproducibility issues for some of the methods they
employ. We see an opportunity for LLMs to help educate researchers about
reproducibility pitfalls across methods and support the validation of research
findings. For example, regarding qualitative methods, which have been subject
to claims of reproducibility, LLMs might provide additional verification
complementing manual data analysis. This also holds an opportunity to counter
the bias of a single or few interpreters analyzing qualitative research data,
as Tabone and de Winter (Tabone and de Winter, 2023) demonstrated. Similarly,
LLMs can support quantitative data analyses by cross-checking and reasoning
about the applicability of statistical tests and the validation of
calculations through a second entity. At the same time, we note the risk of
overreliance on LLMs across HCI research methods. LLMs can help improve
research reproducibility as an assistive tool across various HCI research
methods. Besides providing cross-validation, LLMs can help fill individual
gaps in best practices. Yet, LLMs should carefully be used as a supportive
tool rather than a single source of analysis, bearing the risk of
overreliance, bias, and subsequently irreproducibility.

###  3.4. Defining New Reporting Requirements and Educating the Community

More documentation of data and metadata must be required to represent a key
issue for research reproducibility today. Various initiatives across research
fields attempt to encourage or demand scientists to provide the most accurate
documentation of recording conditions, hardware setups, software
specifications, and many more. The introduction of LLMs into research
practices requires developing new best practices regarding the reporting of
LLM usage. Diverse fields like HCI must specifically investigate and pose
requirements that apply across research methods. We suggest the following:

  1. (1)

Establish precise documentation requirements as part of publication venues
that demand detailed information regarding the scope of LLM use, prompts
entered, and corresponding metadata like concrete LLMs used and their specific
versions.

  2. (2)

Provide accessible educational resources for the wider HCI research community
that explain those reporting requirements and general LLM use challenges such
as bias, hallucination, and value lock-in.

  3. (3)

Contribute to the development and incentivize the use of transparent and
accessible LLMs that provide detailed information on the type of data used for
training and that remain accessible to the community for reproduction. This
targets the primary reproducibility concern that older or specific versions of
commercial and proprietary LLMs become unavailable to the public.

###  3.5. The Risk of Increased Research Pressure on HCI Reproducibility

Researchers face the challenge of producing high-quality research while
ideally generating sufficient output to advance their careers. The use of LLMs
provides an opportunity to increase efficiency. For example, Shaer et al.
(Shaer et al., 2024) demonstrated that LLMs can support creative ideation
processes. Along those lines, Schmidt et al. (Schmidt et al., 2024) envisioned
the partial substitution of human participants through LLMs, and Tabone and de
Winter (Tabone and de Winter, 2023) discussed using LLMs in data analysis and
reporting. These opportunities might create pressure, as Schmidt et al.
(Schmidt et al., 2024) underlined: “By using LLMs, we might make UCD cheaper
and hence more widely applicable; at the same time, though, we put pressure on
the field to move this way to stay competitive. Hence, the transparency about
how UCD is conducted and to what extent models are used is critical.”
Considering the concern of research reproducibility, we must also address the
potential risks associated with the pressure to adopt LLMs. The premature
introduction of LLMs into general HCI research could manifest mispractices
before best practices across the diverse HCI methodologies can be established
and communicated. Moreover, the anticipated increase in paper submissions
could strain an already busy peer review system, potentially impacting the
time reviewers can dedicate to assessing the reproducibility implications of
LLM use. We suggest the following:

  1. (1)

Manage and communicate expectations and address concerns regarding LLM use and
potentially perceived pressure within and across HCI laboratories.

  2. (2)

Develop, communicate, and demand best practices as quickly as possible as part
of paper submission requirements. This might happen through dedicated
workshops and panels at HCI publication venues.

  3. (3)

Educate peer reviewers about best practices and evaluate whether and how LLMs
might support increasingly complex and rich peer review processes, considering
potential pitfalls like bias, hallucination, and value lock-in.

##  4\. Risk or Chance for Reproducibility in HCI?

LLMs present a significant opportunity for HCI research to accelerate data
analysis and disseminate results. While acknowledging the benefits of
employing LLMs to make HCI data analysis procedures more accessible to the
community, it is essential to approach their increasing use cautiously. The
structure, training methodologies, and frequent updates of LLMs are not
designed to yield consistent results, which can affect reproducibility,
manifest biases, and increase pressure on publication processes. This article
suggests a discourse on the influence of LLMs within the HCI community and
their impact on research reproducibility. We aim to generate interest in a
series of focused discussions we plan to organize soon. These conversations
will explore establishing specialized scientific platforms for disseminating
research conducted in this domain, aiming to maintain reproducibility when
employing AI tools for HCI data analysis.

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