Understanding the functional organization of the human mind depends on the type, quality, and particularly the precision of the measurements employed in research. Experimental research in human neuroscience involves multiple steps (designing and conducting a study, data processing, statistical analyses, reporting results) – each involving many parameters and decisions between (often) equally valid options. This so-called ‘garden of forking paths’ during the research process has received considerable attention (Gelman and Loken, 2014), as it has been demonstrated that findings critically depend on design, processing, and analysis pipelines (Botvinik-Nezer et al., 2020; Carp, 2012). Analytical heterogeneity can have a crucial impact on measurement precision (Moriarity and Alloy, 2021) and consequently on statistical power and sample size requirements (Button et al., 2013). In this review, we focus on the often-neglected question of how to optimize measurement precision in human neuroscience and discuss implications for power analyses. Knowledge about these factors will strongly benefit neuroscientists interested in individual differences, group-level effects, and biomarkers for disorders alike as different research questions profit from different optimization strategies. Many of these factors are passed on by lab traditions but are not necessarily well documented in the published literature or evaluated empirically. For example, factors such as the number of trials per condition, tolerance for sensor noise, scanner pulse sequences, and electrode positions are often based on previous work in a given lab rather than a solid quantitative principle. Therefore, there is an urgent need to synthesize the available empirical evidence on the determinants of precision and to make this knowledge available to the neuroscience research community, which requires the sharing of original data using standardized reporting formats (e.g., BIDS, https://bids.neuroimaging.io/specification.html).

We define measurement precision as the ability to repeatedly measure a variable with a constant true score and obtain similar results (Cumming, 2014). Therefore, precision will be highest if the measurement is not affected by noise, measurement errors, or uncontrolled covariates. Crucially, precision is related to yet distinct from other concepts such as validity, accuracy, or reliability (see Figures 1 and 2 for the relation of precision to other concepts and the Glossary in the Appendix for explanations of the most important terms). The higher the precision on a participant- or group-level, the higher the statistical power for detecting effects across participants or between groups of participants, respectively. Thus, a more precise measurement increases the probability of detecting a true effect. Additionally, this results in a more accurate estimation of effect sizes that can be used for future power calculations. Research projects that are based on proper power calculations help to produce less ambiguous results and, ultimately, lead to a more efficient use of research funds.

Figure 1

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Figure 2

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Figure 2—source code 1

Reliability, between & within variance.

This R code simulates four samples of 50 subjects with 50 trials each using different degrees of variability within and between subjects. The results indicate that (odd-even) reliability is best at a combination of low within-subject variance but high between-subjects variability (leading to lower group-level precision). Reliability declines when within- and between-subjects variance are both high or low and is worst when the former is high but the latter is low. The results support the claims illustrated in Figure 2.

https://cdn.elifesciences.org/articles/85980/elife-85980-fig2-code1-v1.zip

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Figure 2—source code 2

Reliability & (between) SD.

This R code simulates two samples of 64 subjects with 100 trials each using vastly different degrees of between-subjects variance (but constant within-subject variability, leading to constant subject-level precision). The results show that, everything else being equal, homogenous samples (i.e., with low between-subjects variance) optimize group-level precision at the expense of reliability (Hedge et al., 2018), while heterogenous samples optimize reliability at the expense of group-level precision.

https://cdn.elifesciences.org/articles/85980/elife-85980-fig2-code2-v1.zip

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Although high measurement precision is a key determinant of statistical power, it has often been neglected. Rather, increasing sample size has evolved as the primary approach to augmenting statistical power in psychology (Open Science Collaboration, 2015) and neuroscience (Button et al., 2013). Generally, statistical power of a study on group differences is determined by the following parameters: (a) the chosen threshold of statistical significance α, (b) the unstandardized effect size relative to the total variance, and (c) the total sample size N. This model can be converted to obtain the total sample size needed to achieve a desired statistical power for simple statistical analyses (e.g., the main effect of an ANOVA), given an expected effect size (e.g., f for ANOVA models) and significance level (Button et al., 2013; G*Power Faul et al., 2009). Numerous researchers have previously called for increased sample sizes in human neuroscience to achieve adequate statistical power (e.g., Button et al., 2013; Szucs and Ioannidis, 2020). However, the cost of acquiring neuroscience data is comparatively high, considering preparation time, consumables, equipment operating costs, staff training, and financial compensation for participants. External resource constraints often render the results of a priori power analyses meaningless if the number of participants cannot be easily increased (Lakens, 2022).

Raising the total sample size is only one possible way to increase statistical power. A promising alternative is to enhance precision at the aggregation level of interest. This can be achieved on group-level by an adequate selection of the sample and/or paradigm (Hedge et al., 2018), on the subject-level by increasing the number of trials (Baker et al., 2021; Boudewyn et al., 2018; Chaumon et al., 2021), or even on the trial-level by using more precise measurement techniques. Conversely, a lack of measurement precision results in an increased amount of error variance and, thus, increases the estimate of total variance. Critically, determining the gain in precision from increasing the trial count is not trivial. While extending the number of participants provides independent observations and predictable merit, additional trials can increase the impact of sequence effects (e.g., habituation, fatigue, or learning). Consequently, increasing the number of trials will not indefinitely benefit measurement precision and reliability (see Figure 2 for a delimitation of both terms), although sequence effects can be mitigated by including breaks or by modeling them (e.g., Sperl et al., 2021).

Measurement precision is beneficial for statistical power in multiple ways. In the following, we compiled a summary of these factors in the context of different biopsychological and neuroscientific methods. We provide information on their possible influence on measurement precision (and related concepts, see Glossary in Appendix) and describe future avenues to quantifying influences of under-researched variables that may affect measurement precision to an unknown degree. We encourage neuroscientists to comprehensively assess and report these determinants in the future, and also to consolidate empirical evidence about the magnitude of their impact on measurement precision. Furthermore, we motivate basic research on this topic to identify conditions in which the influence of certain factors may be particularly important or negligible.

In the following section, we focus on five different neuroscientific and psychophysiological methods to exemplify different aspects related to precision: We begin with magnetic resonance imaging (MRI) to illustrate how the utilization of covariates can reduce error variance. Subsequently, we focus on magneto- and electroencephalography (M/EEG) to explain how aggregation across repeated measures is another option to reduce unsystematic noise. Next is electrodermal activity, which provides a prime example of a change in the signal of interest due to sequence effects (especially habituation). Afterwards, eye-tracking is used to illuminate the interplay of precision and accuracy (Figure 1B). Finally, the impact of biological rhythms on hormone expression is demonstrated in the section on endocrinology. Vitally, the concepts exemplified in each subsection are not specific to the presented neuroscientific method and should thus be considered for every neuroscientific study (more comprehensive information can be found in the Table of Resources in Supplementary file 1). We conclude these sections of the manuscript by identifying seven issues that should be considered to ensure adequate precision when collecting multiple neuroscience measures simultaneously.

Data analysis

Preprocessing

There are various software tools for analyzing MRI data, for example, FSL (Jenkinson et al., 2012), SPM (Ashburner, 2012), FreeSurfer (Fischl, 2012), and AFNI/SUMA (Saad et al., 2004). All analyses require data pre-processing, for which different pipelines have been proposed with regard to both structural (Clarkson et al., 2011) and functional analyses. These pipelines differ, for example, in the quality of normalization of individual brains into a standard space or motion correction (Esteban et al., 2019; Strother, 2006). An essential step to improve precision is to apply thorough quality assessment (QA) methods to the pre-processed data. For structural data, the manual ENIGMA QA protocol (ENIGMA, 2017) or automated quality metrics (Esteban et al., 2017) have been shown to improve data quality (Chow and Paramesran, 2016).

General approach

For the analysis of MRI data, a general linear model (GLM, Friston et al., 1999) is commonly used in a mass-univariate approach (see Figure 3C). Here, precision mainly depends on the data quality and sample composition. Moreover, error variance can be reduced by adding covariates (e.g., participant movement for functional analyses; and age, sex/gender, handedness, and total intracranial volume for structural analyses). Furthermore, physiological noise from heartbeat or breathing can be modeled and, thus, corresponding noise decreased (Chang et al., 2009; Havsteen et al., 2017; Kasper et al., 2017; Lund et al., 2006). Note, however, that the univariate analysis approach has been shown to have inferior retest-reliability compared to multivariate analyses (Elliott et al., 2020; Kragel et al., 2018). For this reason, some researchers generally recommended multivariate over univariate analyses (Kragel et al., 2021; Noble et al., 2019). In addition, the intake of all substances that interact with central nervous activity or blood flow in the brain should be assessed. These are likely to have an effect on fMRI, but there are no general guidelines on how to deal with them. While excluding participants who regularly consume nicotine, alcohol, or caffeine would greatly reduce the generalizability, not accounting for different exposures to these psychoactive substances increases error variance and, thus, reduces measurement precision. Therefore, the level of regular consumption and the time since last intake could be assessed and used as covariate to control for systematic variation in BOLD responses due to the effects of the substance.

Figure 3

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Functional magnetic resonance imaging: Studying brain activation

Functional magnetic resonance imaging data are usually analyzed using a two-level summary approach. First-level models analyze the individual subject’s BOLD time series and estimate summary statistics (such as individual contrast-weighted GLM coefficients, see Figure 3) that are further investigated at the second or group-level (Penny and Holmes, 2004). At the group-level, estimated effects depend on the precision of the subject-level estimations, also benefiting from the previously mentioned use of covariates and random effects (Penny and Holmes, 2004). Furthermore, one can model serial autocorrelation and deviations from the canonical hemodynamic response function, and apply frequency filters that preserve the experimentally induced BOLD signal but reduce error-related signals in first-level analyses (Friston et al., 2007).

In contrast to voxel-wise univariate analyses, multivariate analysis approaches combine information across voxels, for example, to distinguish different groups or to predict behavior (Haxby et al., 2014). Some of these approaches account for large parts of the variance in the predictor space (principal component regression) or in both the predictor and outcome space (partial least squares, Frank and Friedman, 1993). Regularized regression approaches such as elastic nets, LASSO (Least Absolute Shrinkage and Selection Operator) analyses, or ridge regression can serve the same purpose by incorporating information of only few or many voxels (Gießing et al., 2020).

Connectivity and brain networks

The analysis step of parcellation assigns each voxel of the acquired neural data into separate regions of the brain, which are then used as nodes in the network, between which the connections (edges) are estimated. Various parcellation schemes using different criteria such as anatomical landmarks, cytoarchitectonic boundaries, fiber tracts, or functional coactivations to define those network nodes were developed and used in previous research (López-López et al., 2020; Passingham et al., 2002; Schleicher et al., 1999). For the construction of functional brain networks, functional parcellation schemes are often used assigning voxels according to their coactivations (e.g., the Local-Global Schaefer 200, Schaefer et al., 2018) or multimodal templates with consistent boundaries across different modalities (Glasser et al., 2016). In some cases, the original parcellation schemata include only cortical regions and have later been extended to subcortical brain areas (López-López et al., 2020). The choice of the optimal parcellation depends on the specific research question and results should ideally be replicated with different parcellations (Arslan et al., 2018; Bryce et al., 2021). Furthermore, current evidence suggests that analyses of time-resolved functional connectivity might profit from templates developed on patterns of dynamic functional connectivity (Fan et al., 2021).

Thus, precise parcellation is the basis to ensure meaningful connectivity patterns (Zalesky et al., 2010) and using a standard atlas for parcellation facilitates meta-analytic work and increases comparability across various studies. However, previous studies have also shown that functional parcellations of the brain vary from person to person as well as over time (Kong et al., 2019). The use of an individual parcellation template created for each subject at a specific time point separately can improve the prediction of behavioral performance, provided that the individual templates are calculated based on fMRI datasets of sufficient long scanning duration (Gordon et al., 2017; Kong et al., 2021). Another important aspect specific for task-related connectivity is the removal of task-evoked brain activation, which can be achieved by basis set task regression (e.g., Cole et al., 2019). If functional brain networks are analyzed as graphs, global metrics instead of node-specific measures have higher precision (Braun et al., 2012). There are also recommendations for dynamic connectivity analyses (Lurie et al., 2020). The highest temporal precision can be achieved by temporally resolving the correlation metric itself. Such analyses might even allow network construction of every single sample point (Faskowitz et al., 2020; Zamani Esfahlani et al., 2020). Functional brain networks have further been used as input for machine learning-based models to increase measurement precision by ‘learning’ the most relevant features of connectivity (Cwiek et al., 2022; Nielsen et al., 2020).

Concerning measurement precision of structural connectivity analyses, the use of parcellation atlases based on anatomical similarities like the Desikan-Killiany atlas (Desikan et al., 2006) or the Destrieux parcellation (Destrieux et al., 2010) is recommended (Pijnenburg et al., 2021). Multimodal atlases like the HCP Glasser parcellation (Glasser et al., 2016) are preferable when structural and functional connectivity are estimated simultaneously (Damoiseaux and Greicius, 2009; Rykhlevskaia et al., 2008). Structural connections can be modeled based on probabilistic or deterministic tractography and both methods have advantages, while multi-fiber deterministic tractography (or properly thresholded probabilistic tractography) evolved as the best solution (Sarwar et al., 2019). However, even with the gold standard analysis techniques, issues remain if fibers cross within one voxel (Jones et al., 2013; Schilling et al., 2018; Seunarine and Alexander, 2009) or when multiple fibers converge in one voxel and run in parallel before separating again (Schilling et al., 2022) resulting in reduced precision of connectivity estimates. Several approaches for data acquisition or analysis have been suggested to address these issues (Landman et al., 2012; Sedlar et al., 2021). Other issues concern the use of symmetric (recommended) versus asymmetric connectivity matrices, or the correction for node size (as discussed in Yeh et al., 2021).

Electrodermal activity (EDA)

Electrodermal activity reflects eccrine sweat gland activity controlled by the sympathetic nervous system (Bach, 2014) which can be recorded non-invasively by electrodes attached to the skin. The signal is composed of a tonic component (i.e., slow variations in skin conductance level; SCL) and a phasic component (i.e., individual skin conductance responses; SCRs). While SCL is related to thermoregulation and general arousal, SCRs reflect stimulus-induced activation (Amin and Faghih, 2021) characterized by different components such as amplitude, latency, rise time, or half recovery time (Dawson et al., 2016). Despite the existence of closely related measures like skin potential, resistance, or impedance, we exclusively focus on skin conductance here, which is measured in microsiemens (µS).

Hardware, design, and data recording

Comprehensive overviews and guidelines on data recording are available (Boucsein, 2012a; Boucsein et al., 2012b; Dawson et al., 2016). In brief, the skin should be prepared using lukewarm water (no soap, alcohol, or abrasion) and exact electrode placement should be constant between participants – optimally using anatomical landmarks – to reduce error variance (Christopoulos et al., 2019; Payne et al., 2013; Sanchez-Comas et al., 2021; Boucsein et al., 2012b).

For SCRs, which are rather slow responses, a sampling rate of 20 Hz is considered sufficient but higher sampling rates improve measurement precision (Venables and Christie, 1980). SCRs have an onset lag of approximately 1 s after the eliciting stimulus (0.5 s for high intensity stimuli), which has consequences for the temporal spacing between different experimental events. Responses to temporally close events (i.e., <4 s) are inherently difficult to separate due to the resulting overlapping SCRs with possible consequences for measurement precision. Note, however, that deconvolution-based approaches have been developed for these scenarios (Bach et al., 2013; Benedek and Kaernbach, 2010). Importantly, as novel, surprising, or arousing stimuli elicit SCRs, also events of no interest (e.g., startle probes; Sjouwerman et al., 2016) may result in overlapping SCRs.

Some factors with documented impact on SCRs should also be recorded and controlled including demographic variables like age, sex, or ethnic background (Dawson et al., 2016; Webb et al., 2022) as well as medication or scars at the electrode positions (Christopoulos et al., 2019; Payne et al., 2013; Boucsein et al., 2012b). Furthermore, time of day (Hot et al., 2005) as well as environmental factors like room temperature (Boucsein et al., 2012b) and humidity (Boucsein, 2012a) modulate electrodermal activity and should thus be held constant (e.g., between 20 and 26 °C with a 50% humidity; Christopoulos et al., 2019).

SCRs are subject to strong habituation effects (Lykken et al., 1988; for an illustration see Figure 4). Consequently, increasing the number of trials to augment subject-level precision and reliability (Allen and Yen, 2001) is not straightforward for SCRs. Indeed, larger trial numbers did not generally improve reliability estimates of SCRs (in a learning paradigm; Klingelhöfer-Jens et al., 2022). One interpretation of this result is that increasing precision by aggregation over more trials can get counteracted by sequence effects. Relatedly, habituation must also be considered for within-subject manipulations (i.e., more trials per subject, albeit in different experimental conditions) and weighed carefully against the option of between-subjects manipulations, which may induce interindividual differences in SCL and/or electrodermal responsiveness between groups. Notably, individuals with higher SCL show a higher number and larger amplitudes of SCRs (Boucsein, 2012a; Venables and Christie, 1980). Consequently, adaptive thresholding for SCRs may be a means to increase statistical power (Kleckner et al., 2021).

Figure 4

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Figure 4—source data 1

This zip archive contains EDA data (‘eda.txt’) and rating data (‘ratings.csv’), which are loaded and processed in the R script ‘Habituation R’ to reproduce Figure 4.

The R script also contains examples on how to calculate precision for SCL and SCR. The data have been reused with permission from Reutter and Gamer, 2023.

https://cdn.elifesciences.org/articles/85980/elife-85980-fig4-data1-v1.zip

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Data analysis

Processing continuously recorded skin conductance data for analysis of stimulus-elicited SCRs requires a number of steps, all with (potential) relevance to measurement precision including response quantification (see Kuhn et al., 2022; Pineles et al., 2009; Sjouwerman et al., 2016), selection of a minimal response threshold (Lonsdorf et al., 2019) with 0.01 µS used as a quite common consensus criterion (Boucsein, 2012a; but see Kleckner et al., 2021 for an adaptive approach), filtering (Privratsky et al., 2020), as well as standardization for between-subjects comparisons (e.g., range-correction; Lykken and Venables, 1971). Few of these steps have been systematically investigated with respect to measurement precision. Recent multiverse-type work suggests that effect sizes and precision derived from different processing and operationalization steps differ substantially despite identical underlying data (Klingelhöfer-Jens et al., 2022; Kuhn et al., 2022; Pineles et al., 2009; Sjouwerman et al., 2016). Furthermore, exclusion of participants due to non-responding in SCRs is based on heterogeneous definitions with potential consequences on measurement reliability and precision (Lonsdorf et al., 2019).

Reporting standards

Reporting standards are available (Boucsein et al., 2012b) and include details for subject preparation (e.g., hand washing, skin pre-treatment), data recording (e.g., hard-/software, filter, sampling rate, electrode placement, electrode and gel type, temperature and humidity), data processing (e.g., filter, response quantification details including software and exact settings used, time windows, transformations, cut-offs, non-responder criterion) as well as justifications for the choices.

Eye-tracking

Eye-tracking is the measurement of gaze direction based on the pupil position. We will focus on pupil and corneal reflection methods using infrared light as the currently dominant technology (Duchowski, 2017) but most conclusions are also valid for other applications. Eye-tracking takes an exceptional position in this list of neuroscientific methods as accuracy (Figure 1 or Glossary in Appendix) can be readily quantified as the difference between the recorded gaze position and the actual target’s coordinates (Hornof and Halverson, 2002). Consequently, there is a strong focus on calibration and validation procedures that measure errors of the system (Figure 5). In the eye-tracking literature, ‘precision’ refers specifically to trial-level precision (Glossary in Appendix; Holmqvist et al., 2012) of the time series signal during fixations. Another important index of data quality is the percentage of tracking loss, indicating the robustness of eye-tracking across the temporal domain (Holmqvist et al., 2023).

Figure 5

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Design and data recording

Setup-specific factors

Assembling an eye-tracking environment, several factors need to be considered to retain adequate precision. For example, the eye-tracker must have a high sampling rate of at least 200 Hz to prevent an increase in sampling error (Andersson et al., 2010). In addition, distances within a setup should be chosen wisely. Firstly, the operating distance (between participant and eye-tracker) directly affects pupil detection and thus precision and accuracy (Blignaut and Wium, 2014). Secondly, a larger viewing distance (between participant and observed object) decreases the precision of derived measures by diminishing the stimulus image on the retina (i.e., in degrees of visual angle) and thus increases the risk of misclassification in region-of-interest (ROI; also ‘area-of-interest’, AOI) analyses (Vehlen et al., 2022). Since vertical accuracy is usually worse than horizontal, the height-to-width-ratio of the stimuli should also be considered (Feit et al., 2017).

Procedure-specific factors

Several factors should be considered prior to data collection. Since accuracy is best in close proximity to the calibration stimuli (Holmqvist et al., 2011), their number and position should be chosen to correspond to the area encompassed by experimental stimuli (Feit et al., 2017). Furthermore, movement of the participant can influence data quality. Although highly dependent on the eye-tracker model, head movement can also affect both accuracy and precision, either through a loss of tracking in remote eye-tracking (Niehorster et al., 2018) or through slippage in mobile eye-tracking (Niehorster et al., 2020). Additionally, a change in viewing distance after calibration can lead to a parallax error (lack of coaxiality of camera or eye-tracker and eyes), threatening the accuracy of the gaze signal (Mardanbegi and Hansen, 2012).

Participant-specific factors

Facial physiognomy can affect the quality of the eye-tracking data. For example, downward pointing eye lashes and smaller pupil size decrease accuracy; narrow eyes decrease both accuracy and precision (Blignaut and Wium, 2014) while effects of mascara are debated (Nyström et al., 2013). Data precision of participants with blue eyes was lower than that of participants with brown eye color for infrared eye-trackers (Hessels et al., 2015; Nyström et al., 2013). Visual correction aids influence eye-tracking data quality: Contact lenses decrease accuracy, while glasses decrease precision (Nyström et al., 2013).

Endocrinology

Hormones are chemical messengers produced in endocrine glands. They exert their effects by binding to specific receptors (Ehlert and Känel, 2010) and thereby affect various psychological processes (Erickson et al., 2003), which, in turn, may influence hormone concentrations (Sunahara et al., 2022).

Hormones are measured in body fluids and tissues, including blood, saliva, hair, nails, stool, and cerebrospinal fluid. Yet, measures across these measurement domains may reflect different outcomes: While some indicate the current biologically active hormone availability termed acute state (e.g., saliva cortisol), others represent cumulative measures building up over time, termed chronic state (e.g., hair cortisol; Gejl et al., 2019; Kagerbauer et al., 2013; Sugaya et al., 2020; Vining et al., 1983). Critically, samples of different domains often require different sampling devices (Gallagher et al., 2006), handling, and storage conditions (Polyakova et al., 2017; Toone et al., 2013). The adherence to recommendations regarding hormone- and measurement-specific factors is therefore essential to maintain hormone stability, and thus measurement precision (see Resources in Supplementary file 1).

Hormone concentrations are determined with biochemical assays relying on microtiter plates, specific reagents, and instruments. In addition to assay-specific sensitivity and specificity, inter- and intra-assay variation of any given analysis directly relate to measurement precision (El-Farhan et al., 2017). Intra-assay variability refers to the variability of hormone concentrations across identical samples (duplicates) on the same microtiter plate, whereas inter-assay variation refers to the variability across identical samples on different microtiter plates. Many factors can contribute to high variability, such as variation in preprocessing steps (Szeto et al., 2011). Therefore, samples of one study should be analyzed at a single laboratory (ideally in duplicates), with constant protocols, and biochemical reagents from the same manufacturer and charge, thus minimizing variability related to assay components (so-called ‘batch effects’, Leek et al., 2010).

Design

A precise measurement of hormone-dependent effects on psychological processes and vice versa requires exact timing of sampling. Often, the collection of hormone samples has to be scheduled with respect to an intervention or event of interest (Stalder et al., 2016) and considering lagged and dynamic hormone responses (Schlotz et al., 2008). Some hormones show early or acute effects on psychophysiological processes that differ entirely from later or delayed effects (Weckesser et al., 2019).

When hormonal dynamics are considered a confound, collecting hormone samples over multiple time points can increase measurement precision (Sunahara et al., 2022; see Figure 6B, Box 3). However, some hormone concentrations do not necessarily change over a certain time (Born et al., 2002), thereby limiting the utility of additional hormone samples in these cases.

Figure 6

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Besides lagged responses, biological rhythms lead to substantial variability in hormone concentrations that may impair measurement precision (Haus, 2007; Figure 6A). While some biological rhythms account for circular hormone changes within just minutes or hours (e.g., circadian rhythm, Figure 6A), hormone concentrations also change within months, seasons, or years (Barth et al., 2015; e.g., puberty or menopause).

Particular attention should also be paid to factors that disrupt biological rhythms. For example, shift work or jet lag typically disrupt diurnal rhythms (Bedrosian et al., 2016), while medication such as oral contraceptives disrupt lunar rhythms and confound physiological endpoints beyond rhythmicity (Brønnick et al., 2020; Fleischman et al., 2010). This additional variation can greatly reduce or even reverse effect sizes (e.g., Shields et al., 2017).

Besides external factors that might disrupt biological rhythms, there are also endogenous shifts in hormone regulation, for example, age-dependent changes related to developmental phases (i.e., puberty and menopause). This variability can confound measures of underlying individual differences in hormonal concentrations. It can be controlled by restricting the target population or by explicitly comparing and statistically accounting for individual development stages. Finally, attention has to be paid to confounds like seasonal fluctuations (Tendler et al., 2021) that impair measurement precision in longitudinal study designs.

Biological rhythms also exist across various modalities including neuroimaging data and receptor activity (Barth et al., 2015; McEwen and Milner, 2017; Orban et al., 2020; Pritschet et al., 2020), with hormones often acting as a driving force (Arélin et al., 2015; McEwen and Milner, 2017; Taylor et al., 2020). Inclusion of hormonal concentrations in statistical analyses can partially control for this variability (e.g., Cheng et al., 2021).

Besides biological rhythms-related confounds, numerous lifestyle and environmental factors affect the variability of hormone concentrations and may limit measurement precision. Although a complete list of potential confounds is beyond the present scope, the most important factors are those with a potential influence on hormone regulation, such as physical and mental health conditions (Adam et al., 2017), medication (Montoya and Bos, 2017), drug, nicotine, and alcohol consumption (Kudielka et al., 2009).

Data analysis

Hormone data rarely fulfill the assumptions underlying parametric procedures such as homoscedasticity and normal distribution. Rather than resorting to less powerful non-parametric procedures, data transformations can be used to counteract violations of assumptions (Miller and Plessow, 2013). However, these data transformations must be applied with caution (e.g., Feng et al., 2013). Moreover, hormone data often exist as time series; directly analyzing the repeated measures instead of comparing aggregated scores usually conveys higher analytical sensitivity (Shields, 2020). Time series data further allow the statistical modeling of lagged hormone effects, which can also enhance analytical sensitivity (Weckesser et al., 2019).

Analytical sensitivity can be further increased by building statistical models that capture the nature of hormone effects, which frequently manifest in interaction rather than main effects (Bartz et al., 2011). These effects must be adjusted for potential confounds, either by considering them as factors or covariates in the models. Switching from between- to within-subject designs can also help to increase analytical sensitivity of the models (van IJzendoorn and Bakermans-Kranenburg, 2016), which typically require large sample sizes to be sufficiently powered to detect the effects of interest (Button et al., 2013).

Reporting standards

Despite recent calls to improve the rigor and precision in hormone research (e.g., Quintana et al., 2021; Winterton et al., 2021), there is a lack of guidelines describing how hormone findings should be presented (Meier et al., 2022). However, careful documentation of the study design, participant sample with all inclusion and exclusion criteria, type of hormone sample(s) and device(s), time of sample collection, storage procedure with preprocessing steps, and assay type with corresponding inter- and intra-assay variation obtained in the analyses (not the coefficients reported by the manufacturer) is highly recommended.

While we have presented precision-related considerations separately for many psychophysiological and neuroscientific methods, it is common to use multiple methods within a single study. Combining different methods allows the assessment of different levels of response, which typically tap into different manifestations of the underlying construct and hence provide complementary insights. For example, it is reasonable to assume that activation in a particular brain area (e.g., the amygdala) precedes and thus predicts a peripheral physiological (e.g., EDA) or behavioral response (e.g., arousal rating). However, there are a number of inherent challenges and specific considerations in combining multiple measures, both in general and in terms of precision.

First, measurement specific idiosyncrasies may impact the to-be-studied process. For example, it has been shown that ‘triggered’ responses, e.g., ratings and startle electromyography (EMG), which require distinct event onsets such as a question or an eliciting tone, can impact the to-be-studied (cognitive) process – for instance by hampering a learning process (Atlas et al., 2022; Sjouwerman et al., 2016).

Second, the recording of multiple measurement modalities may interfere with each other on a purely technical level. For example, when examining SCRs to pictures in combination with tones designed to elicit a startle reflex measured by EMG, the startle evoking tones will not only elicit an EMG blink response but also phasic SCRs. If the sequence and timing of the experimental stimuli (e.g., pictures and tones) are not explicitly tailored to take into account both modalities, they may interfere with each other. The resulting overlap between SCR-responses to stimuli of interest (e.g., a picture) and stimuli of no interest (e.g., tones) may in the worst case preclude meaningful analyses. Similarly, what is a necessary prerequisite for one measurement modality (e.g., eye movements for eye-tracking) may have a detrimental effect on the measurement precision of another measurement modality (e.g., distortion of EEG signals caused by eye movements). Other examples include cardioballistic artifacts in the EEG signal (induced by pulse-related head movements in the magnetic field, Allen et al., 2000, when EEG and fMRI are recorded simultaneously). Similarly, verbal responses during BOLD fMRI acquisition can increase noise in the fMRI signal (Barch et al., 1999). While in some cases it may be possible to correct the signal for such interferences, for example by recording ECG to subtract cardioballistic artifacts from simultaneous EEG/fMRI recordings (Allen et al., 2000), using specific algorithms to detect deviations from the average EEG signal (Allen et al., 2000; Niazy et al., 2005), or independent component analysis (Debener et al., 2007; Mantini et al., 2007), it is usually best to avoid them in the first place through experimental design and specifically tailored experimental timing (e.g., collecting button presses rather than verbal responses in the MRI scanner).

Third, because measurement modalities have inherently different properties, it can be challenging to decide on how to optimize the experimental paradigm to achieve the best possible overall precision. For example, as mentioned above, the gain in precision from increasing the number of trials is not trivial. While increasing the number of participants provides additional independent observations and thus predictable merit, additional trials are subject to sequence effects (e.g., habituation, fatigue, reduced motivation, or learning). For example, while a high number of trials may be beneficial for increasing precision in EEG (Baker et al., 2021; Boudewyn et al., 2018; Chaumon et al., 2021), such a high number of trials may decrease precision in EDA due to strong habituation of SCRs. For example, to capture responses prone to habituation, ‘dishabituation’ can be achieved by adding novel stimuli (Sperl et al., 2021). Another solution could be to pre-register the optimal number of trials per measurement modality and only include this number of trials in subsequent analyses. However, this may not be feasible for studies with a learning element as early and late trials may tap into different stages of a process that is expected to change over time (Sperl et al., 2021).

Fourth, because different measures inherently differ in precision they also differ in statistical power. Using behavioral performance as the basis for calculating power and sample size estimations for neuroscientific methods is likely to be misleading. This might result in underpowered studies that threaten scientific progress (Button et al., 2013).

Fifth, when investigating associations between two different measures, it is important to keep in mind that the precision of the least precise measurement determines the upper boundary of an observable relationship. More specifically, the correlation between two variables cannot exceed the smallest reliability exhibited by any of the two variables (Spearman, 1910). Using multiple read-out measures in a single study comes with the inherent challenge of determining whether the same or different hypotheses exist for different measurement modalities and, in the former case, the extent to which that hypothesis can be considered confirmed if only one of these modalities shows the expected effect. In fact, such divergent findings may be related to precision being optimized for one measurement modality but less so for another. Furthermore, in the case of different predictions for different measurements, a correction for multiple comparisons is generally not necessary (Feise, 2002), whereas controlling for Type I (alpha) error may be warranted if the hypothesis is considered to be confirmed if the effect is observed in one out of several outcome measures.

Sixth, pseudo-relationships between two measurements can arise from related secondary variance between these measurements. For example, head movement may simultaneously affect both EEG and MRI measures, leading to similarities in their signals. These could introduce spurious correlations between the EEG and MRI data even in the absence of a meaningful conceptual relationship between them (Fellner et al., 2016).

Seventh, when analyzing time series data from multiple neuroscientific measurement modalities together, it is important to allow for precise synchronization in the time domain during acquisition. This is easier to achieve if the two signals are acquired by the same device (e.g., EEG and EOG by the same amplifier, or MRI and peripheral physiology by the same MRI scanner). If this is not possible, precision can be optimized by ensuring that all devices are synchronized in clock time (Bullock et al., 2021; Mandelkow et al., 2006; Xue et al., 2017). Software solutions for device synchronization exist (e.g., Lab Streaming Layer) and are being augmented by efforts to provide low-cost hardware solutions (Bilucaglia et al., 2020). This issue is also very important to consider when performing hyper-scanning studies (Babiloni and Astolfi, 2014; Barraza et al., 2019). In addition, precision can be further improved by considering brain time instead of clock time to synchronize neuroscientific measurements between participants according to ongoing oscillatory brain dynamics (van Bree et al., 2022).

As we have argued throughout this review, the precision of psychophysiological and neuroscientific methods is affected by a number of technical, procedural, and data analysis steps. Increasing precision improves the estimation of statistical effects, largely independent of the costs associated with increasing sample size. This has important implications for how we conduct and evaluate power analyses, as several aspects beyond sample size must be considered and compared across studies when basing a power analysis on previous research: How were measurements protected from unsystematic influence? Was similarly precise technical equipment used? Were appropriate designs and robust participant preparation procedures applied? Is the number of trials comparable across studies? What preprocessing steps were taken to decrease noise? What covariates were recorded and included in the analysis? Critically, the exact extent to which these steps impact precision and statistical power is currently largely unknown and needs to be systematically evaluated in the future.

Planning for precision at the level of interest

One advantage of considering measurement precision is the explicit reference to levels of aggregation: Are we studying group-level differences or associations with subject-level estimates? Within this framework, it becomes more intuitive how different research questions require precision at their respective levels of aggregation (i.e., group- or subject-level).

More specifically, different optimizations of certain variance components may come in handy: For group differences, reducing between-subjects variance (within the same groups) increases precision at the group level for a given sample size (Hedge et al., 2018). For correlational hypotheses, however, the between-participant variance should be maximized to stabilize the relative positions between subjects (given constant subject-level precision, Figure 2). Consequently, the ‘two disciplines of scientific psychology’ (Cronbach, 1957), that is, experimental psychology and correlational psychology in Cronbach’s terms, require different optimization strategies with respect to between-subjects variance.

Less controversial, on the other hand, is the role of within-subject variance: This component should usually be minimized to increase the precision at the subject-level. For correlational hypotheses, this decreases error variance by definition (Glossary in Appendix: Reliability). For group differences, high subject-level precision carries on to improve group-level precision (Baker et al., 2021), providing a win-win scenario for statistical power and reliability. Indeed, precision can be viewed as a one-way street, with trial-level precision carrying on to improve subject-level precision, which in turn improves precision at the group aggregation level (see Figure 7). To this end, the merit of increasing sample size is strictly limited to group-level precision, with no benefit to subject-level estimates or reliability. Consequently, in the absence of further information on the efficiency of increasing precision on different levels, priority should be given to optimizing trial-level precision.

Figure 7

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Figure 7—source code 1

This R code can be used to reproduce Figure 7.

https://cdn.elifesciences.org/articles/85980/elife-85980-fig7-code1-v1.zip

Download elife-85980-fig7-code1-v1.zip

In the glossary, we define core concepts relevant to this review. We acknowledge that these definitions may vary between different disciplines in human neuroscience.

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