Abstract
Blood oxygen level-dependent functional magnetic resonance imaging (fMRI) is a widely used, non-invasive method to assess brain hemodynamics. Resting-state fMRI (rsfMRI) estimates functional connectivity (FC) by measuring correlations between the time courses of different brain regions. However, the reliability of rsfMRI FC is fundamentally compromised by statistical artifacts arising from signal cyclicity, autocorrelation, and preprocessing-induced distortions.
We discuss how standard rsfMRI preprocessing —particularly the widely used band-pass filters such as 0.009–0.08 Hz and 0.01–0.10 Hz— introduce biases that increase correlation estimates between independent time series. Additionally, filtering without appropriate downsampling further distorts correlation coefficients, inflating statistical significance and increasing the risk of false positives. Under these conditions, commonly used multiple comparison corrections fail to fully control Type I errors, with up to 50–60 % of detected correlations in white noise signals remaining significant after correction depending on the sampling rate, filter and duration.
To mitigate these biases, we recommend adjusting sampling rates to align with the analyzed frequency band and employing surrogate data methods that better account for the statistical properties of rsfMRI signals and reduce autocorrelation-driven false positives. Additionally, we show that structured brain states—such as epilepsy and anesthesia-induced burst suppression—impose low-frequency neural activity that further amplifies these biases, distorting FC estimates.
These findings indicate that accepted rsfMRI preprocessing pipelines systematically amplify spurious correlations and call for an improved statistical framework. This framework must explicitly account for autocorrelation, cyclicity, and multiple comparison biases, while excluding or correcting for structured neural activity that further distorts connectivity estimates.
1. Introduction
Resting-state functional MRI (rsfMRI) is a cornerstone of modern neuroimaging, widely considered to provide insights into brain network organization by inferring functional connectivity (FC) from correlations in blood oxygenation level-dependent (BOLD) signals. While rsfMRI holds promise for mapping brain networks non-invasively (Biswal et al., 1995; Logothetis, 2008; Logothetis et al., 2001; Raichle, 2010; Greicius et al., 2003) compared to previous invasive approaches to studying hemodynamics (Cooper et al., 1966), its diagnostic applications, particularly at the individual patient level, remain challenging due to unresolved statistical limitations. Despite significant methodological advancements (Raimondo et al., 2021; Yang et al., 2020; Buckner et al., 2013), fundamental issues persist, including the cyclicity inherent in biological signals, inflated statistical significance, and ambiguities in defining the resting state (Marek et al., 2022; Gratton et al., 2020).
The motivation for this review is to examine how statistical challenges limit the utility of rsfMRI, focusing specifically on processes that introduce complications into FC analysis. Accordingly, key neurophysiological factors, such as brain vasomotion and neuronal oxygen consumption, are considered solely in terms of their contribution to cyclicity and noise that distort rsfMRI-derived metrics.
Previous recent reviews (Raimondo et al., 2021; Buckner et al., 2013; Drew et al., 2020) have addressed the theoretical basis of rsfMRI or its broad clinical applications, but this review uniquely focuses on the statistical limitations that constrain its research and diagnostic potential. By analyzing the impact of cyclic biological signals and confounding brain states such as epilepsy, burst suppression, and stress, we propose statistical solutions to improve the reliability of rsfMRI-derived metrics.
At its core, fMRI captures the dynamics of deoxyhemoglobin (Buxton, 2013), linked to blood flow, blood volume, and blood oxygenation. These hemodynamic processes are governed by brain vasomotion and neuronal oxygen consumption. Vasomotion, defined as spontaneous or event-driven oscillations in blood vessel diameter, plays a central role in regulating cerebral blood flow. However, its cyclic nature introduces significant statistical challenges for interpreting rsfMRI-derived FC.
This review bridges the gap between theoretical statistical challenges and their practical implications for rsfMRI, offering a framework for addressing these limitations through a combination of refined definitions and advanced statistical methodologies. A key statistical challenge in analyzing cyclic data, such as rsfMRI signals, is the presence of autocorrelation, which is further exacerbated by the use of narrow bandpass filters. While preprocessing methods are commonly employed to mitigate these effects, their theoretical justification remains tenuous. For example, pre-whitening, a widely used approach, assumes a specific autoregressive noise model, but its effectiveness in rsfMRI remains debated (Cliff et al., 2021).
To address these challenges, alternative methodologies such as Fourier Transform-based surrogate data analysis provide an empirical solution by preserving the auto-correlative properties of the data (Lancaster et al., 2018) in order to construct more accurate null distributions for the correlation statistic (; ). Unlike preprocessing methods, surrogates require no assumptions about the underlying noise structure, making them a robust tool for assessing the impact of preprocessing on FC estimates.
This review is structured to systematically examine these issues. First, we explore key statistical challenges in rsfMRI, particularly the need for more robust hypothesis testing in the presence of cyclicity and autocorrelation. Next, we discuss the limitations of traditional statistical corrections, including the shortcomings of correction for multiple comparisons, and emphasize the critical role of sampling rate selection in mitigating bias. We also examine alternative analytical approaches, such as Granger causality, coherence analysis, and pre-whitening, assessing their effectiveness in rsfMRI.
Beyond methodological considerations, we evaluate the diagnostic potential of rsfMRI at the individual patient level under traditional analytical frameworks and highlight the growing role of machine learning approaches in improving reliability. Additionally, we discuss the impact of confounding physiological and pathological factors—such as anesthesia, epilepsy, and stress—on resting-state recordings, and propose stricter operational definitions of the resting state to improve reproducibility.
Through this comprehensive review, we aim to provide a clear statistical framework for improving the reliability of rsfMRI FC analysis, ensuring that preprocessing choices do not systematically inflate false positives or distort biological interpretations.
2. Statistical analysis of resting state correlates: implications for accidental correlations
The analysis of resting-state functional MRI (rsfMRI) data involves a variety of methods. High-dimensional imaging and electrophysiological data, combined with the complexity of underlying neurovascular interactions, introduce numerous confounds into the analytic process. Advanced methods, such as machine learning models, can uncover non-linear relationships (Khosla et al., 2019), while dimensionality reduction techniques like independent component analysis (ICA) are used to identify latent variables driving aggregate behavior (Mwangi et al., 2014). For examples on the application of ICA see (Beckmann et al., 2005; Griffanti et al., 2017; Griffanti et al., 2014). Although these methods are effective for generating regions of interest (ROIs) for time courses, they do not alter the underlying cyclicity of biological signals.
In this chapter, we focus on challenges related to the statistical analysis of cyclical biological signals, assuming proper application of the previously mentioned analytical techniques. We review cross-correlation, a typical statistical method in rsfMRI, along with additional approaches such as corrections for multiple comparisons, Granger causality analysis, and surrogate data methods.
2.1. Calculation of correlations
2.1.1. Correlation coefficients in fMRI
Highlights:
Correlation coefficients (CC) are a fundamental metric in rsfMRI for assessing linear relationships, and is expressed as FC in the context of comparing distinct brain regions. However, CCs only measure association, not causality, and are prone to spurious correlations due to unaccounted external influences or inherent cyclicity of the signals.
Correlation coefficients are a straightforward approach to quantifying the linear relationship between datasets. Each CC is paired with a p-value, representing the probability of observing the given value under the null hypothesis. FC is defined as the correlation of hemodynamic patterns (Linnman et al., 2012) between distinct brain regions. FC is expressed as a correlation coefficient with an associated p-value, often used to infer interactions between neuronal populations based on the similarity of their BOLD signal time courses. Although, other methods of human brain mapping exist, such as using geometric eigenmodes to more accurately account for the topological characteristics of the brain (Pang et al., 2023), this review will focus on the voxel-based FC metric, which is commonly employed for rsfMRI studies.
Although widely used, correlation coefficients are limited in their ability to determine causal relationships for several reasons:
No Directionality: CCs do not specify the direction of causality (e.g., whether region A influences region B or vice versa).
Unrecorded Variables: A third, unmeasured process may drive the observed dynamics of both signals, leading to spurious associations.
Coincidence: Similar variations in two datasets may arise purely by chance rather than reflecting a true functional relationship (Cliff et al., 2021).
These limitations are particularly concerning in neurovascular coupling and long-range FC research, where spurious correlations can misrepresent the actual neurophysiological interactions. For example, a correlation between hemodynamic activity in two regions may not necessarily indicate meaningful neuronal connectivity but could result from systemic noise or unrelated background oscillations (Cliff et al., 2021; Schaworonkow et al., 2015)).
Consider two fMRI signals from different brain regions that exhibit similar time-course fluctuations due to a shared neurophysiological process, such as spontaneous vasomotion (Rayshubskiy et al., 2014) occurring at similar frequencies. These signals may demonstrate high correlation coefficients (CCs) despite the absence of a direct functional relationship between the regions. Such spurious correlations, driven by shared systemic or physiological noise rather than genuine connectivity, pose significant challenges when interpreting FC maps, particularly in clinical and research contexts.
While CC remains a practical and widely used method in rsfMRI, its inability to infer causality and susceptibility to spurious correlations highlight the need for complementary methods that can provide greater robustness and accuracy in understanding brain network interactions. In contrast, causality-driven methods, such as Granger causality analysis, offer directionality and temporal dependency modeling that may clarify the underlying functional architecture beyond simple correlation-based analyses (Seth et al., 2015).
2.1.2. Caveats related to correlation coefficients
Highlights:
Correlation coefficients in rsfMRI analysis are prone to spurious significance due to the cyclic nature of biological signals and the impact of autocorrelation. Addressing these issues requires robust statistical methods, such as surrogate data approaches, rather than relying on data alteration techniques like pre-whitening.
The chance of recording correlations by accident is tested explicitly through the use of a null distribution, which is the distribution of correlations assuming the null hypothesis is true. It is commonly accepted that the null distribution for (studentized) Pearson correlations, assuming the underlying variables are independent, is well approximated by the Student’s t-distribution (Rahman, 1968). The null distribution is used for hypothesis testing, where p-values are calculated and significance is determined. Both electrophysiological and hemodynamic data have a strong cyclical component, and hence cannot be considered independent data with respect to time (Bollmann et al., 2018; Fiecas et al., 2017). We define the cyclical component as the component of a signal which generates repetitive patterns, though not necessarily in a periodic fashion, in accordance to (Shahsavarani et al., 2019). Cyclicity in data will cause an upward bias in the variance of the sample correlation estimate, which makes the standard t-distribution ill-suited for significance testing. In other words, the likelihood of a sample containing a large correlation is higher than can be explained by the standard null distribution, meaning many statistically significant correlations will be actually due entirely to chance (Davey et al., 2013).
Consider two time-series signals with an underlying dominant cyclical frequency of 0.01 Hz. If these signals are analyzed without accounting for their cyclical nature, they may exhibit a significant Pearson correlation simply because of phase alignment at certain intervals, even if no causal relationship exists. This spurious correlation results from the cyclical structure of the data rather than meaningful connectivity between the signals.
Furthermore, the sampling rate of the fMRI signal can, paradoxically, increase the chance of recording a significant correlation by accident (Corbin et al., 2018; James et al., 2019), if the dominant frequency of the signal is considerably smaller than the sampling rate. For example, when the correlation between two signals is driven by an auto-correlative process (Fig 1), an excessively high number of time points will only lower the p-value for significance while retaining a similar correlation value. This artificially inflates the significance of correlation coefficients due to the increased sample size, which tightens the null distribution. As a result, the corresponding t-statistic becomes higher, thus lowering the p-value of the correlation value.
Fig. 1.
The effect of sampling rate on the p-value of correlation coefficients. When the sampling rate exceeds what is needed to adequately describe the information content of the signal, it artificially inflates the statistical significance of correlations. This example illustrates three distinct signals: the first oscillates at a frequency of 1.5 cpm (black), the second also oscillates at 1.5 cpm but with a phase shift relative to the first signal (orange), and the third consists of multiple oscillations at frequencies of 0.2 cpm, 0.5 cpm, 1.4 cpm, and 1.5 cpm with randomized phases (red).
At the original sampling rate of 1 Hz, all three signals (A-C) show significant correlations with each other at the Bonferroni-corrected level. However, when the sampling rate is reduced to 0.1 Hz, comparisons among the signals (D-F) reveal no correlations that pass the Bonferroni significance threshold (p ≤ 0.0167). Notably, the actual relationships between the signals remain unchanged, as the sampling rate has minimal impact on the correlation coefficients themselves in these oscillation frequencies. Instead, the inflated p-values in the 1 Hz sampling condition are due to the excessive sample size. This example underscores the importance of aligning the sampling rate with the signal’s intrinsic information content to avoid artificially inflated statistical significance.
To eliminate this issue, we suggest reducing the sampling rate whenever possible, using methods such as power spectrum analysis to identify the appropriate bandwidth of the signal. By doing so, the dynamics of the signal are retained without the artificial inflation of the t-statistic. This approach effectively reduces the chance of accidentally inflated correlations.
Despite these challenges, correlation analysis remains one of the most practical methods for identifying neurophysiologically meaningful relationships between neuronal activity and rsfMRI. With the application of advanced statistical approaches, such as surrogate data methods, it is possible to enhance the robustness of FC analysis even in the presence of cyclicity and autocorrelation.
2.1.3. Preprocessing methods to address autocorrelation
Highlights:
Pre-whitening does not appear to be an effective solution for reducing autocorrelation bias in FC analysis of rsfMRI data, particularly in the presence of bandpass filtering. Several alternative preprocessing techniques attempt to reduce autocorrelation, but all present trade-offs between signal integrity and bias reduction.
In fMRI studies, pre-whitening is applied to reduce the effect of autocorrelation on correlation estimates. The most popular fMRI processing packages (AFNI, FSI, and SPM) have the functionality to pre-whiten data (Olszowy et al., 2019). There exist many different specific pre-whitening methods, but the principle is to remove the auto-correlative component between two sets of data, which is typically done using an using autoregressive (AR) or auto-regressive moving average (ARMA) models. Previous reviews discuss the various methodologies of pre-whitening, going into the specifics of which ARMA filter to use, depending on brain region of interest (Olszowy et al., 2019; Parlak et al., 2022). Interestingly, a previous study used pre-whitening to correct for auto-correlation in rsfMRI data and concluded that autocorrelation has a limited impact on the correlations used in FC analysis (Arbabshirani et al., 2014). However, a recent paper found that auto-correlation greatly affects FC and that pre-whitening does not reliably remove auto-correlative bias; in certain cases, it may even exacerbate the bias (Cliff et al., 2021).
The apparent discrepancy between these studies stems from their differing focuses and assumptions: the earlier study (Arbabshirani et al., 2014) primarily assessed the impact of autocorrelation on group-level FC statistics, operating under the assumption that pre-whitening sufficiently removed autocorrelation, without directly quantifying the extent of residual autocorrelation in individual time series after preprocessing. Based on this assumption, the study reported that correlations did not change significantly after pre-whitening and concluded that autocorrelation had a limited effect on cross-correlations. However, if pre-whitening does not fully remove autocorrelative bias within the time series, the stability of cross-correlations remains compromised, and the conclusions of the study become invalid. In contrast, the latter study (Cliff et al., 2021) demonstrated that standard pre-whitening techniques are insufficient to eliminate autocorrelation bias, particularly in measures of statistical dependence such as FC, highlighting the ongoing influence of autocorrelation even after preprocessing.
Pre-whitening applied in the context of bandpass-filtered rsfMRI data presents an inherent conceptual conflict. When pre-whitening is performed before filtering, it is largely ineffective because the subsequent bandpass filter imposes new autocorrelation by restricting the signal to a narrow frequency band, re-introducing auto-correlation in the signal, regardless of whether the original autocorrelation was removed. On the other hand, applying pre-whitening after filtering (as is common in typical FC analysis pipelines) is theoretically possible but practically ineffective, because the filtering process has already restricted the signal to a narrow frequency band where strong autocorrelation arises as a direct consequence of the limited frequency content. In such cases, there are few meaningful degrees of freedom left for whitening to correct, and any attempt to remove this inherent autocorrelation risks distorting or eliminating the actual signal of interest. In both cases, the benefit of pre-whitening is minimal, as the dominant low-frequency fluctuations induced or preserved by filtering cannot be fully removed without also erasing the signal of interest.
Moreover, the effectiveness of pre-whitening depends critically on the model used to estimate and remove autocorrelation. If the pre-whitening model is overly aggressive—for example, by overfitting the autocorrelation structure—it risks eliminating genuine neural signal components along with noise, effectively "flattening" the meaningful dynamics of the data and undermining the very purpose of connectivity analysis. We demonstrate how standard AR-based pre-whitening methods can remove genuine correlations between two signals of interest (Fig S1 in the Supplement), which is consistent with previous studies (Blanco et al., 2018). Conversely, if the model is too simplistic or underfits the autocorrelation structure, it may fail to sufficiently remove the bias introduced by autocorrelation and shared amplitude modulations, rendering the pre-whitening procedure largely ineffective. This tradeoff highlights why pre-whitening, while commonly assumed to be helpful in practice, lacks strong justification in the context of filtered rsfMRI data and may provide little practical value as a safeguard against spurious correlations.
ICA is frequently employed in rsfMRI to separate neural and non-neural sources of variability, including motion artifacts and physiological noise (Beckmann and Smith, 2004). Potentially, ICA could be used to reduce autocorrelation by identifying and regressing out components associated with slow signal fluctuations. However, this approach is highly dependent on the chosen decomposition method and component selection criteria, making it inconsistent across studies and unlikely to fully eliminate filtering-induced biases.
Specifically, ICA decomposes signals into statistically independent components but does not explicitly remove autocorrelation from the remaining time series. Because autocorrelation is an inherent property of rsfMRI signals—particularly after bandpass filtering—ICA does not prevent spurious connectivity arising from temporal dependencies (Laumann et al., 2015). Studies have shown that low-frequency fluctuations persist even after ICA-based denoising, suggesting that ICA fails to remove residual autocorrelation (Griffanti et al., 2017).
There is no standardized method for determining which ICA components should be removed. Researchers often rely on heuristics, visual inspection, or automated classifiers, which vary between studies and introduce significant variability in results (Kelly et al., 2010; Parkes et al., 2018). This lack of consistency reduces the reproducibility of ICA-based preprocessing. ICA-derived noise components may still contain meaningful neural signals, and arbitrary removal of components can distort FC estimates (Griffanti et al., 2017).
Even when ICA removes structured noise, it does not address the filtering-induced autocorrelation that inflates correlation coefficients and leads to false-positive connectivity (A. Eklund et al., 2016). Since ICA is often combined with standard multiple comparison corrections (such as FDR), which fail to control Type I errors under autocorrelation, it provides no safeguard against statistical inflation (A. Eklund et al., 2016). ICA-denoised signals still exhibit inflated correlation values due to residual low-frequency noise, suggesting that it does not effectively prevent spurious FC findings (Bright and Murphy, 2015).
Different ICA algorithms (e.g., FastICA, Infomax, MELODIC) can yield slightly different component decompositions, leading to inconsistencies across studies (Himberg et al., 2004). Additionally, the stochastic nature of some ICA implementations can produce different results between runs, making ICA-based preprocessing less reliable for large-scale or clinical applications (Salimi-Khorshidi et al., 2014). These limitations suggest that while ICA can be useful for removing structured noise, it does not provide an effective solution for filtering-induced statistical biases in rsfMRI.
Temporal differencing, or first-order differencing, involves computing the difference between consecutive time points, thereby removing low-frequency drifts that contribute to autocorrelation (Zarahn et al., 1997). This method has been explored as a way to reduce temporal dependencies in fMRI signals, with the goal of improving statistical inference (Lund et al., 2006).
Potentially, temporal differencing can be used to reduce autocorrelation in rsfMRI by removing slowly varying signal components that contribute to artificial correlations. However, this approach has several limitations. First, while it can reduce long-range dependencies, it does so at the cost of eliminating meaningful low-frequency fluctuations, potentially discarding valid neuronal information (Bullmore et al., 1996). Second, temporal differencing amplifies high-frequency noise, which can introduce additional artifacts into FC estimates. This tradeoff complicates its application in rsfMRI, where both low-frequency fluctuations and noise contribute to the observed signal.
Moreover, temporal differencing does not provide a solution to filtering-induced autocorrelation but rather shifts the statistical problem by altering the spectral composition of the rsfMRI signal. Since bandpass filtering already constrains the frequency content of the data, applying temporal differencing afterward can introduce distortions that further obscure the true connectivity patterns. As a result, this method remains an imperfect solution for addressing autocorrelation bias in rsfMRI preprocessing and may not be suitable as a standalone correction.
Wavelet-based methods offer a flexible approach for addressing autocorrelation by decomposing rsfMRI signals into multiple frequency components, allowing for the selective removal of those associated with long-range dependencies (Chang and Glover, 2010; Bullmore et al., 2003). This approach has been used in fMRI denoising to separate neural fluctuations from physiological and scanner-related noise while preserving temporal structure (Fadili and Bullmore, 2002).
Potentially, wavelet-based techniques could be applied to reduce autocorrelation in rsfMRI by identifying and removing the frequency components most responsible for spurious correlations. Some studies have implemented wavelet-based filtering to minimize non-neuronal signal contributions, such as respiration and cardiac pulsations, which can influence FC estimates (Patel and Bullmore, 2016). However, a significant limitation of wavelet detrending is the difficulty in precisely defining which frequency bands correspond to noise versus meaningful neural activity. Unlike predefined frequency cutoffs used in conventional bandpass filtering, wavelet-based methods require an adaptive thresholding approach, which can introduce inconsistencies across datasets and study designs.
Additionally, wavelet transformations may distort temporal features of the BOLD signal, particularly if aggressive filtering is applied. Since rsfMRI FC depends on the temporal coherence of signals between brain regions, excessive modification of frequency content can obscure or artificially enhance connectivity patterns (Achard et al., 2006). Moreover, while wavelet-based techniques can help mitigate slow drifts and structured noise, they do not directly address the inflation of false positives introduced by standard bandpass filtering, nor do they eliminate the need for proper multiple comparison corrections.
Hemodynamic deconvolution techniques attempt to remove vascular lag effects and better isolate neural activity (Glover et al., 2000). These methods assume that the observed BOLD signal is a convolution of underlying neural activity with a hemodynamic response function (HRF), which can be estimated and inverted (Boynton et al., 1996; Gitelman et al., 2003). By deconvolving the HRF, researchers aim to recover a neural signal that is less confounded by slow hemodynamic fluctuations, which can contribute to autocorrelation in rsfMRI data.
In principle, HRF deconvolution could be used to mitigate autocorrelation by removing low-frequency components introduced by the sluggish response of the vasculature. Studies have attempted to model subject-specific HRFs to improve the accuracy of FC estimates (Handwerker et al., 2004). However, the effectiveness of this approach depends heavily on the accuracy of the HRF model used. The HRF varies across individuals, brain regions, and brain states, meaning that incorrect assumptions about its shape can introduce artifacts rather than correcting autocorrelation (Aguirre et al., 1998).
Furthermore, HRF deconvolution is limited by noise amplification. Since deconvolution is effectively an ill-posed inverse problem, small errors in HRF estimation can lead to large distortions in the recovered neural signal (Logothetis and Wandell, 2004). This issue is exacerbated in rsfMRI, where the absence of clear task-driven responses makes HRF estimation more difficult compared to task-based fMRI studies. Moreover, deconvolution does not address filtering-induced autocorrelation; it only aims to correct for hemodynamic lag, leaving other statistical biases unresolved.
Thus, while HRF deconvolution provides a potential means of reducing vascular confounds, its practical utility in addressing filtering-induced statistical biases remains questionable. Given the inherent variability in HRF across individuals, it may not serve as a reliable solution to autocorrelation artifacts in rsfMRI data. For more detailed reviews on preprocessing methods see (Lee et al., 2013; Shereena and Raju).
These findings emphasize the need for more robust hypothesis-testing methods that explicitly account for autocorrelation, rather than relying on data alteration techniques such as pre-whitening. Methods such as surrogate data and downsampling approaches offer a promising alternative for addressing cyclicity and autocorrelation bias.
2.2. Correction for multiple comparisons and its role in cyclic signals
Highlights:
Corrections for multiple comparisons is effective for independent data but struggles with cyclical signals such as those typical for rsfMRI.
Correcting for multiple comparisons is a widely used technique in rsfMRI studies, since the matrix of voxels or ROI’s can be quite large, increasing the likelihood of recording a low p-value by chance (Lindquist and Mejia, 2015). This correction involves adjusting the significance level (alpha) to account for multiple hypothesis testing, reducing the risk of false positives.
In general, Bonferroni and Holm-Bonferroni corrections are widely used, with Bonferroni being the more conservative approach (Breznik et al., 2020). However, in rsfMRI analysis, the standard approach is false discovery rate (FDR) correction, specifically the Benjamini-Hochberg method, as it is widely assumed to balance false positive control with statistical power.
For example, the Bonferroni method achieves correction by dividing alpha by the number of comparisons, thereby lowering the p-value threshold required for statistical significance. While Bonferroni correction is designed to control false positives under standard conditions, it assumes that the null distribution accurately represents the true null hypothesis. Its application in large-scale rsfMRI analyses is generally considered conservative.
However, the effectiveness of correction methods diminishes when applied to cyclical data. In these cases, the tails of the null distribution are often larger than the Student’s t-distribution (Davey et al., 2013; James et al., 2019). One prominent and well-established source of cyclicity is vasomotion, a vascular process characterized by spontaneous or event-driven oscillations in the diameter of cerebral blood vessels, particularly arterioles (Hudetz et al., 1998; Aalkjaer et al., 2011) (for other sources see Section 2.3). Vasomotion occurs independently of external influences such as cardiac pulsation or respiration and plays a fundamental role in regulating cerebral blood flow and ensuring adequate oxygen and nutrient delivery to brain regions, particularly those remote from large blood vessels (Doubovikov and Aksenov 2020; Goldman and Popel, 2001; Tsai and Intaglietta, 1993).
Studies have shown that localized vasomotion oscillates at frequencies 0–20 cpm (0–0.333 Hz) (Linsenmeier et al., 2016; Manil et al., 1984; Aksenov et al., 2018; Mateo et al., 2017; Rivadulla et al., 2011; Dirnagl et al., 1989), with a peak frequency, for example, near 10 cpm (0.166 Hz). While these oscillations are critical for normal brain function and serve as a protective mechanism against hypoxic damage (Doubovikov and Aksenov 2020), they also introduce a strong cyclical component into the BOLD signal (see Section 2.5). The cyclic nature of vasomotion introduces substantial bias into the statistical analysis of FC, as it strongly influences the rsfMRI signal (Rayshubskiy et al., 2014). Addressing these biases is essential to fully harness the diagnostic potential of rsfMRI.
Bonferroni correction, while widely used for controlling false positives in multiple comparisons, does not address biases introduced by cyclicity in time-series data. These biases violate the assumption of independence underlying the p-values, resulting in misleading conclusions even after correction. Time-series data, such as rsfMRI signals, often exhibit strong temporal dependencies and cyclical components, which can inflate correlation coefficients and compromise the validity of null distributions used for hypothesis testing.
Returning to the example from Section 2.1.2, two time-series signals exhibited significant Pearson correlations due to accidental phase alignment at certain intervals. Could Bonferroni correction account for this error? While it may seem so, as Bonferroni correction is applied to p-values, this logic is fundamentally flawed. The p-value of the correlation is influenced by the sampling rate, which can artificially increase the number of data points without adding meaningful information. High sampling rates tighten the null distribution and reduce the standard error of the correlation coefficient, leading to deceptively lower p-values. As a result, spurious correlations are more likely to pass the Bonferroni correction threshold, giving a false impression of significance.
Fig. 1 demonstrates how Bonferroni correction fails to determine significance appropriately in cases where the sampling rate is too high. In rsfMRI, the cyclicity induced by vasomotion not only biases the null distribution but also increases the likelihood of spurious correlations, challenging the validity of multiple comparison corrections like Bonferroni. This limitation underscores the challenges of applying Bonferroni correction to time-series data dominated by auto-correlative processes.
Addressing these challenges requires alternative statistical approaches that account for the periodic nature of rsfMRI data. Surrogate data methods, which preserve the cyclic properties of biological signals when generating null distributions, provide a promising avenue for robust hypothesis testing. By accounting for the basis of cyclicity, such as vasomotion, these methods can mitigate the limitations of traditional correction techniques and improve the reliability of rsfMRI-derived FC metrics.
2.3. Enhanced correlation bias due to filtering
Highlights:
From a statistical perspective, low-pass filtering in rsfMRI artificially introduces auto-correlation, inflates variance in correlation estimates, and reduces effective degrees of freedom, thereby increasing the risk of spurious FC findings.
Resting-state fMRI signals and their low-frequency fluctuations remain a topic of ongoing debate regarding their origins. Two primary hypotheses dominate this discussion:
Oxygen Consumption Hypothesis – Suggests that low-frequency fluctuations in FC reflect oxygen metabolism (Raichle, 2006). However, supporting evidence remains inconclusive, as resting-state neuronal activity does not appear to drive significant changes in oxygen dynamics (Zhang et al., 2021).
Vasomotion Hypothesis – Proposes that cyclic low-frequency oscillations in blood flow, rather than oxygen consumption, shape rsfMRI signals (Rayshubskiy et al., 2014; Rivadulla et al., 2011; Tong et al., 2019; Yuen et al., 2019). Several studies have demonstrated a strong relationship between neuronal activity and vasomotion (Mateo et al., 2017) or blood flow and rsfMRI (Tong et al., 2017), supporting this perspective.
Spontaneous vasomotion has traditionally been considered non-neuronal (Rayshubskiy et al., 2014; Aksenov, 2021; Munting et al., 2023; Lambers et al., 2023). However, since studies typically observe vasomotion without blocking neuronal activity, it remains unclear whether these fluctuations arise independently or are partially driven by neural signals. Vasomotion can exhibit similar frequencies across multiple brain regions, potentially creating artifactual connectivity in rsfMRI. Furthermore, neuronal activity has been shown to modulate higher-frequency vasomotion (Mateo et al., 2017; Yuen et al., 2019), suggesting that at least some aspects of vasomotion may not be purely spontaneous.
Some researchers view vasomotion as an unwanted source of noise that should be excluded from rsfMRI analysis. These researchers often assume that vasomotion occurs primarily at frequencies above 0.1 Hz (Yuen et al., 2019) and that neuronal/metabolic processes underlying rsfMRI signals are distinct from vasomotion. However, findings from Mateo et al. (Mateo et al., 2017) challenge this assumption by demonstrating that vasomotion occurs within a broad frequency band centered near 0.1 Hz, meaning it partially overlaps with the frequency range typically retained in rsfMRI (0.01–0.1 Hz).
This raises a critical concern: bandpass filtering below 0.1 Hz may inadvertently exclude relevant neuronal signals while still retaining components of spontaneous, non-neuronal vasomotion (Doubovikov and Aksenov 2020). As a result, this filtering could alter the balance of neural and non-neuronal contributions to rsfMRI FC, affecting data interpretation.
This interplay between neuronal and non-neuronal vasomotion, along with oxygen consumption dynamics, raises fundamental questions about the true neurophysiological basis of FC at low frequencies. Distinguishing between these contributions is essential for accurately interpreting resting-state FC results and ensuring that observed correlations reflect neural activity rather than physiological artifacts.
To address physiological noise, rsfMRI data is commonly bandpass-filtered to retain fluctuations within the 0.01–0.1 Hz range (Drew et al., 2020; Krishnan et al., 2018). This filtering is intended to remove high-frequency physiological noise, which dominates above this range (for review, see (Murphy et al., 2013)). However cardiac (~0.04 Hz; (Akselrod et al., 1981)) and respiratory (~0.03 Hz; (Wise et al., 2004)) signals still fall within the filtered range, raising an important question: What physiological signals are actually removed by this filter, and what remains?
This paradox becomes especially apparent when considering vasomotion. The commonly used 0.01–0.1 Hz bandpass filter retains part of the vasomotor spectrum while discarding other physiologically plausible signals, an issue even more pronounced with the narrower 0.009–0.08 Hz filter. Vasomotion can potentially span a broad frequency range, from near 0 Hz to above 0.3 Hz (Linsenmeier et al., 2016; Manil et al., 1984; Aksenov et al., 2018; Mateo et al., 2017; Rivadulla et al., 2011; Dirnagl et al., 1989), with its peak often near or above 0.1 Hz. Filtering below 0.1 Hz (or 0.08 Hz) preserves only the slowest component of vasomotion, regardless of whether it is neural or non-neural, while removing faster fluctuations that may include meaningful neural contributions. As a result, these filters neither eliminate vasomotion entirely nor isolate neural activity with any physiological specificity. Instead, they retain an arbitrary slice of low-frequency structure that can introduce shared temporal features across brain regions, artificially inflating functional connectivity estimates.
Beyond the unclear neuro-physiological justifications, filtering rsfMRI data introduces substantial statistical implications. One major issue is that low-pass filtering inherently increases autocorrelation, even if the original data were uncorrelated (Arbabshirani et al., 2014; Lindquist et al., 2019). Auto-correlation inflates the variance of correlation estimates, reducing the effective degrees of freedom for hypothesis testing and biasing FC estimates (Davey et al., 2013; Bright et al., 2020). Since rsfMRI signals already exhibit strong cyclicity, filtering further amplifies this bias, artificially increasing correlations between unrelated brain regions (Hallquist et al., 2013; Power et al., 2012).
While previous studies have acknowledged that bandpass filtering can induce spurious correlations, no prior work has systematically examined the extent to which these artifacts persist after FDR correction using purely independent noise data. Most analyses have focused on raw correlation inflation, but the effectiveness of standard statistical adjustments like FDR in this context has not been explicitly shown. Given that FDR is widely assumed to control Type I errors and is incorporated into commonly used neuroimaging software packages such as FSL, AFNI, SPM, DPABI, and GRETNA, it is critical to evaluate its reliability in rsfMRI preprocessing pipelines.
To address this gap, existing methodological concerns regarding filtering effects were systematically examined using purely independent white noise signals. By applying standard rsfMRI preprocessing pipelines, we review and present quantitative evidence on false positive inflation at each processing stage, before and after FDR correction, revealing the extent to which filtering artifacts distort statistical significance (Table 1).
Table 1.
Effect of Bandpass Filtering on False Positive Rates in White Noise Correlations Before and After FDR Correction. Comparison of the proportion of significant p-values before and after FDR correction for 0.01–0.1 Hz and 0.009–0.08 Hz bandpass filters.
| Duration (min) |
Sampling Rate (Hz) |
Filter Order |
Raw Before FDR ( %) |
Raw After FDR ( %) |
Filtered (0.01–0.1 Hz) Before FDR ( %) |
Filtered (0.01–0.1 Hz) After FDR ( %) |
Filtered (0.009–0.08 Hz) Before FDR ( %) |
Filtered (0.009–0.08 Hz) After FDR ( %) |
|---|---|---|---|---|---|---|---|---|
| 5 | 1 | 4 | 5.033 | 0.006 | 57.635 | 52.698 | 64.198 | 60.826 |
| 30 | 1 | 4 | 5.046 | 0.005 | 47.691 | 40.019 | 54.843 | 49.11 |
| 5 | 1 | 2 | 5.009 | 0.012 | 55.324 | 49.729 | 62.016 | 58.182 |
| 30 | 1 | 2 | 4.985 | 0.004 | 45.999 | 37.725 | 53.043 | 46.918 |
| 5 | 0.5 | 4 | 5.025 | 0.004 | 32.414 | 19.388 | 39.899 | 29.535 |
| 30 | 0.5 | 4 | 5.072 | 0.003 | 26.627 | 11.797 | 33.04 | 20.039 |
| 5 | 0.5 | 2 | 4.98 | 0.01 | 32.505 | 19.531 | 40.035 | 29.596 |
| 30 | 0.5 | 2 | 4.936 | 0.003 | 26.409 | 11.792 | 32.953 | 19.951 |
Table 1 was generated by simulating independent white noise signals and computing pairwise correlations before and after applying a bandpass filter using a standard double filtering approach commonly employed in rsfMRI preprocessing. See the supplement for the details.
The results in Table 1 illustrate how standard rsfMRI preprocessing pipelines significantly impact false positive rates in rsfMRI analyses. Before filtering, independent white noise time series yield approximately 5 % significant p-values, as expected under the null hypothesis, with FDR correction reducing FPR to near 0 %. However, after filtering, the proportion of significant correlations drastically increases, reaching 50–60 % for 5-minute recordings and 40–50 % for 30-minute recordings before FDR correction. This underscores the need to critically re-evaluate filtering strategies, as these artifacts are introduced even in completely uncorrelated signals.
Despite the widespread reliance on FDR correction to control multiple comparisons, filtering-induced false positives remain unacceptably high even after correction—persisting at ~50 % for shorter recordings and ~38–40 % for longer recordings. This suggests that common statistical controls may be inadequate for rsfMRI preprocessing pipelines, raising concerns about the reliability of standard FC estimates.
Table 1 indicates the following trends:
Lowering the sampling rate (0.5 Hz vs. 1 Hz) reduces false positives but does not eliminate them, suggesting that improper sampling exacerbates statistical inflation.
Applying a narrower bandpass (0.009–0.08 Hz) further inflates false positives, confirming that the choice of filter parameters significantly influences statistical bias. Notably, this specific bandpass range has recently gained popularity, underscoring the importance of scrutinizing its effects.
Table 1 was validated using both an autoregressive (AR(1)) model (Table S1) and empirical human rsfMRI data from the Human Connectome Project (Table S2). Empirical data revealed alarmingly high false-positive rates—up to 60 %—following bandpass filtering. These findings highlight a fundamental methodological issue in standard rsfMRI preprocessing: bandpass filtering does not merely reshape frequency content; it actively induces spurious correlations that significantly distort functional connectivity estimates. The persistent inability of standard statistical corrections (such as FDR) to adequately mitigate these artifacts underscores the necessity of alternative strategies, including proper downsampling or surrogate-based validation methods. Such refinements are crucial to ensure that rsfMRI connectivity analyses reliably reflect genuine neural interactions rather than methodological artifacts.
To advance methodological rigor in rsfMRI analysis, we advocate for the use of independent white noise signals and, where applicable, AR(1) processes (Davey et al., 2013), as a reproducible baseline to systematically quantify the statistical distortions introduced by standard preprocessing. Unlike previous studies that assessed filtering effects using empirical rsfMRI data or surrogate signals derived from actual recordings, these null models offer fully controlled conditions. White noise serves as an assumption-free reference with no temporal structure, ensuring that any observed correlations arise solely from preprocessing choices rather than biological confounds. The AR(1) model complements this by simulating structured, but non-interacting, signals with intrinsic autocorrelation, thus providing a more realistic yet still connectivity-free baseline. Prior studies relying on real or synthetic fMRI data introduce uncertainties due to unknown degrees of autocorrelation, vascular effects, and neuronal interactions, making it difficult to isolate preprocessing artifacts. In contrast, simulations using white noise and AR(1) processes allow the statistical consequences of filtering and sampling to be measured directly and reproducibly.
Given the widespread reliance on standard preprocessing pipelines, we propose that testing with white noise, and, when appropriate, AR(1) processes, should become a routine methodological check in FC studies. These null models provide a principled way to identify whether filtering, sampling, or other steps introduce systematic statistical distortions in the absence of true signal. Incorporating such tests would strengthen the validity of inferred connectivity patterns and enhance the overall reliability and reproducibility of rsfMRI research.
2.4. Downsampling as a principled post-filtering correction
Highlights:
Downsampling after filtering is essential to mitigate inflated correlations caused by oversampling of smoothed signals. Filters like 0.01–0.1 Hz reduce signal bandwidth, making lower sampling rates more appropriate for valid inference. Without downsampling, standard statistical corrections may fail to eliminate spurious correlations. Despite its importance, downsampling is often omitted from rsfMRI preprocessing pipelines.
In signal processing, it is standard practice to downsample a signal after low-pass or bandpass filtering to prevent oversampling of smoothed data (Oppenheim and RW., 2014; Crochiere and Rabiner, 1983). Once high-frequency components are attenuated, the original sampling rate becomes unnecessarily high relative to the retained frequency content. This mismatch can inflate statistical estimates by increasing the apparent degrees of freedom, particularly in correlation-based analyses. Resting-state fMRI pipelines often apply temporal filters (e.g., 0.01–0.1 Hz) but omit subsequent downsampling, inadvertently allowing oversampled smooth signals to produce spurious correlations. We demonstrated (Table 1, Fig. 1, Table S1, Table S2) that this oversight can substantially distort functional connectivity estimates, even under standard statistical correction, and that downsampling is a mathematically necessary corrective step to restore statistical validity.
A bandpass filter of 0.01–0.1 Hz preserves signal components within a limited frequency range, and the Nyquist-Shannon sampling theorem dictates that the sampling rate must be at least twice the upper cutoff to avoid aliasing (Oppenheim and RW., 2014). For a 0.1 Hz upper cutoff, this minimum is 0.2 Hz. However, in most rsfMRI pipelines, zero-phase (double-pass) filtering is applied, which sharpens the filter response and steepens roll-off near the cutoff frequency. This narrows the effective transition band and increases the influence of artificially smooth components just below the cutoff (e.g., near 0.1 Hz), potentially preserving correlations that would otherwise be attenuated. As a result, a 0.2 Hz sampling rate becomes a soft downsampling step: statistically motivated and sufficient to reduce oversampling, but still cautious enough to retain higher temporal resolution (e.g., 12 samples per minute). This approach is particularly useful when data quantity is constrained, such as in short scans or pediatric and neonatal imaging, where aggressive downsampling could render the data unusable.
By contrast, aggressive downsampling refers to lowering the sampling rate further (typically below 0.1 Hz). For instance, with a filter range of 0.009–0.08 Hz and zero-phase (double-pass) filtering, the effective filter may become sharper, and a more conservative downsampling rate (e.g., 0.1 Hz) may be warranted. This ensures suppression of high-frequency leakage and tighter control of statistical inflation, but it comes at the cost of reduced temporal resolution (e.g., only 6 samples per minute). When datasets are short or irreplaceable, such aggressive downsampling may be impractical. In these cases, soft downsampling followed by surrogate-based inference offers a statistically defensible compromise.
To quantify the effectiveness of downsampling in mitigating spurious correlations, we simulated white noise and AR(1) processes (two standard null models with no true connectivity). After applying a 0.01–0.1 Hz bandpass filter, spurious correlations emerged due to the smoothness introduced by filtering (Table 1). Without downsampling, false positives often exceeded 50 %, even after FDR correction. However, applying downsampling to 0.2 Hz substantially reduced the inflation (Table S1, S2).
Under appropriate downsampling, the expected false positive rate before FDR correction should align with the nominal significance threshold (~5 %) in null models. This indicates that downsampling neither removes meaningful variance nor overcorrects the data. Persistent inflation above this level prior to FDR correction suggests residual oversampling or filter-induced correlation structure. After applying FDR correction, the false positive rate should approach zero. Any residual elevation at this stage may reflect lingering artifacts or intrinsic autocorrelation, and may justify the application of surrogate-based inference to ensure robust statistical control. In this regard, downsampling is a simple, effective, and principled correction that directly addresses these statistical inflation concerns. Importantly, while higher acquisition rates (e.g., multi-band, multi-echo methods) offer valuable physiological and methodological benefits, proper downsampling after filtering remains statistically essential for typical low-frequency rsfMRI analyses. Because the bandpass filter has already removed high-frequency components, subsequent downsampling cannot inadvertently remove or damage these components, as they are no longer present in the signal.
These findings align with prior reports of elevated false-positive rates in neuroimaging due to inadequate correction for autocorrelation, spatial smoothness, and overfitting. For example, Eklund et al. (2016) demonstrated inflated spatial extent errors in cluster-based inference; Varoquaux, (2018) and Poldrack et al. (2020) highlighted vulnerabilities in cross-validation and predictive modeling; and Mumford and Nichols, (2008) and Nichols and Hayasaka, (2003) emphasized the importance of accounting for temporal dependencies and multiple comparisons. These observations are consistent with broader concerns about model dimensionality, overfitting, and control of statistical inference in neuroimaging pipelines, as emphasized by Smith et al. (2011). Our contribution extends this literature by isolating a specific pipeline vulnerability, post-filter oversampling, and showing that downsampling mitigates it under true-null conditions, even before any statistical correction. This reinforces calls for principled preprocessing pipelines when computing functional connectivity in rsfMRI. Critically, the methodological inflation identified in our analyses is not dependent on, nor significantly mitigated by, common denoising methods aimed at reducing physiological noise, motion artifacts, or scanner drift. Rather, the inflation arises intrinsically from the statistical properties introduced by standard preprocessing steps (filtering and oversampling), as confirmed by our synthetic analyses and further validated empirically using the Human Connectome Project dataset (Table 1 and Table S1,2).
Permutation testing and surrogate data analysis are two widely used nonparametric approaches for addressing statistical bias in neuroimaging. Permutation tests generate null distributions by shuffling group or condition labels across subjects or observations, assuming exchangeability across samples. This method is particularly effective for group-level inference and classification tasks, and is implemented in commonly used tools such as PALM or FSL-based workflows (Winkler et al., 2014). However, its validity depends on the assumption that samples are independent or exchangeable—an assumption often violated in rsfMRI due to temporal autocorrelation introduced by filtering or oversampling.
Surrogate data methods offer a complementary solution, particularly in the context of autocorrelated or cyclic time series. These methods preserve certain features of the original signal (e.g., spectral content or autocorrelation structure) while disrupting specific statistical dependencies, providing a way to estimate the null distribution of correlation or synchrony under structured noise. This makes surrogate analysis especially appropriate for rsfMRI pipelines affected by temporal filtering.
Together, permutation testing and surrogate analysis highlight the importance of matching the inferential method to the data structure. In our view, preprocessing corrections such as downsampling are essential not only to reduce inflated correlations, but also to ensure that the assumptions behind both parametric (e.g., Random Field Theory (RFT)) and nonparametric (e.g., permutation) methods remain valid.
Another widely used approach for multiple comparison correction in neuroimaging is RFT. RFT provides parametric estimates of the likelihood of spatial clusters arising under the null hypothesis, accounting for the smoothness of brain maps. Implemented in tools such as SPM and FSL, RFT-based corrections are foundational to many fMRI analysis workflows. However, recent work (e.g. (A. Eklund et al., 2016)) has demonstrated that violations of RFT assumptions, such as mismatched smoothing kernels or non-stationarity, can lead to inflated false-positive rates. While our manuscript does not challenge the RFT framework directly, it highlights how upstream preprocessing choices (such as failing to downsample after filtering) can introduce temporal and spatial autocorrelations that compromise the validity of cluster-based inference. We therefore recommend that RFT be applied only after ensuring statistical independence and proper spectral structure through validated preprocessing steps. We emphasize that surrogate methods do not replace traditional multiple comparison corrections (FDR, Bonferroni, or spatial clustering methods). Rather, they serve as an essential upstream step, validating the correlation estimates entering subsequent statistical corrections, thereby ensuring the robustness and validity of downstream inferential methods. Future research should investigate interactions between surrogate-based preprocessing corrections and advanced inferential frameworks (e.g., cluster-based inference, mixed-effects modeling).
2.5. Analysis of cyclic signals
Highlights:
Granger causality provides a powerful tool to infer directional relationships but requires careful handling of autocorrelation and filtering issues. Coherence offers a frequency-domain alternative to cross-correlation, less affected by noise but still vulnerable to biases introduced by low-pass filtering. Filtering choices, especially low-pass filters, can obscure processes like vasomotion, complicating interpretation of rsfMRI data.
Granger causality has become an increasingly popular method in analyzing the physiology of fMRI. Unlike a Pearson correlation, which quantifies linear relationships, Granger causality (G-causality) aims to determine the degree to which one variable "predicts" another (Seth et al., 2015; Wang et al., 2020). This is achieved by fitting a vector auto-regressive (VAR) model on a dependent variable Y, which includes the lagged values of an independent variable X.
In the context of this review:
Y represents an fMRI time-course.
X could represent an electrophysiological signal, such as the firing rate of a single unit or the envelope of an LFP band.
If the error of the VAR model output (Ŷ) increases sufficiently when the lagged X values are removed, we conclude that X “G-causes” Y. The null distribution for the test statistic is well-approximated by the chi-squared distribution.
The main benefit of granger causality over a cross-correlation is that the VAR model controls for the auto-correlation factor, and thus allows for a statistically stronger comparison on the causal nature of two separate processes.
Preprocessing decisions, including filtering, are critical in rsfMRI analysis to reduce noise and isolate specific frequency bands of interest. However, filtering can distort Granger causality by removing key frequency components critical for causal inference, artificially inflating predictability by suppressing high-frequency variability, and obscuring the timing and lag structure essential for detecting true causal relationships. In the absence of pre-processing granger causality is a strong method to determine directionality in FC relationships, however, similar to the specification of the ARMA model in pre-whitening, the selection of lag orders for the VAR model introduces a bias-variance tradeoff, which can generate spurious results (Stokes and Purdon, 2017). In the case that the maximum lag time is too long, the model risks being overfit, while on the other hand, too short of a time lag risks ignoring causal connections over a longer lag (Shojaie and Fox, 2022). There exist various approaches to determine the appropriate time lag, such as regularization approaches using Lasso regression (Shojaie and Michailidis, 2010) or Akaike Information Criterion (AIC) methods (Guo et al., 2010). Furthermore, VAR models require the assumption of stationarity, which is not guaranteed for rsfMRI time courses (Fox et al., 2011). Granger causality also presents challenges with interpretability as the causality estimate is determined independently of the dynamics of the receiver variable (Stokes and Purdon, 2017). Other methods to determine directionality include Bayes net methods, which use the concept of conditional independence, and Patel’s tau, which uses higher order statistics to determine asymmetries in the probability distributions of different areas of activation between brain regions (Wang et al., 2017), and effective connectivity, which using a combination of Bayesian and machine learning methods measures directional relationships between unobserved neural states (Greaves et al., 2025). Probabilistic approaches, using statistical modelling tools such as Stan, also show promise in inferring the spatial map of large-scale brain networks (Hashemi et al., 2020). Effective connectivity and other mechanistic models can provide more beneficial insights in practice than a standard Granger causality method, by modelling the underlying neural dynamics which drives hemodynamics.
Another method of comparison of the similarity between two time series is using coherence. Unlike cross-correlation, coherence measures similarity of the signals via the frequency space, as opposed to the time space. The benefit of coherence over correlation is that it can potentially capture a relationship between two signals invariant of any time lag, which is expected to occur when measuring electrophysiology and rsfMRI. Coherence degrades with noise less in comparison to correlation (Guevara and Corsi-Cabrera, 1996). Although two signals may have a similar power spectrum it may not reflect a causal relationship, since either the auto-correlative process of each signal may be intrinsic or caused by a third unrecorded source. This problem becomes more pronounced when applying stringent low-pass filters. The variability in power from higher frequencies is removed, which can increase the bias of the coherence measure. This becomes more problematic for stricter band pass filters, as narrow filters strongly impose artificial dependencies between time series, inflating coherence values and creating misleading statistical inference (Cliff et al., 2021).
Both Granger causality and coherence are valuable tools for rsfMRI analysis, but their validity depends on appropriate preprocessing choices. Filtering decisions must balance the need to reduce noise with the risk of excluding or overemphasizing specific frequency components. Improper filtering can obscure critical neurophysiological signals, inflate spurious correlations, or distort directional metrics like Granger causality. Careful consideration of these trade-offs is essential for robust and reliable connectivity analysis in rsfMRI.
2.6. Surrogate data
Highlights:
Surrogate data generation preserves key statistical properties (e.g., autocorrelation) while allowing rigorous hypothesis testing in rsfMRI and electrophysiological data. Amplitude Adjusted Fourier Transform (AAFT) surrogates are particularly effective for testing accidental correlations. A multi-step approach that includes surrogate-based null distributions and adjusted statistical thresholds can reduce biases caused by multiple comparisons and large experiment counts.
A more fundamental approach to the testing of accidental correlations is to use bootstrapping and create a new null distribution more tailored to the type of data being analyzed. Bootstrapping refers to the class of methods that seek to estimate the properties (e.g. variance) of a statistical measure by randomly resampling from the sample data. Popular bootstrapping methods include permutation and shuffling, which are well suited when the underlying data is independent and identically distributed (Good, 2005). For rsfMRI and electrophysiological data, however, those methods will destroy any auto-correlative properties of the data. Surrogate data generation encompasses class of methods which use the sampled time series to generate new randomly generated time series that preserve some underlying statistical property (e.g. auto-correlation), to estimate the null distribution of a desired test statistic (G. Lancaster et al., 2018). In this section, we focus on AAFT surrogates, which provide a rigorous statistical framework for testing rsfMRI data and electrophysiological signals combined with rsfMRI (Theiler et al., 1992). Surrogate methods such as AAFT are particularly valuable due to their robust statistical foundations, extensively validated across diverse physical and physiological time-series analyses (G. Lancaster et al., 2018).
AAFT surrogates are created by converting time series data from the time domain into the frequency domain and randomizing the phases to preserve the power spectrum of the original data, along with using Gaussian normalization and a de-Gaussianization of the original time series in the first and last steps, respectively, to preserve the amplitude. The correlation between the AAFT surrogate and the original time series will represent a correlation from two completely independent processes with the same auto-correlative properties. Repeating this process for a specified number of iterations (e.g., N = 1000) generates a distribution of accidental correlations, which serves as a null distribution for hypothesis testing.
Using surrogate data for rigorous hypothesis testing provides significant advantages, particularly when the number of experiments is limited. Surrogate-generated null distributions offer a more accurate approximation of the true population-level null distribution by accounting for wider tails caused by accidental phase matching of similar cyclical properties. It is important to note that transformations, such as Fisher z-scores, should be applied for hypothesis testing because the range of correlation values is constrained between −1 and 1. Since surrogate data provides a more accurate approximation of the null distribution, a correction for multiple comparisons is recommended when analyzing a large number of regions of interest or electrophysiological variables. Fig. 2 and Table S1 show the efficacy of surrogate data to construct an accurate null distribution for band-pass filtered data, using artifical data constructed using an AR(1) model as an example. The proposed workflow (Fig. 3) integrates key preprocessing steps, including justified filtering, downsampling, and surrogate data validation, ensuring that detected FC estimates are not artifacts of preprocessing choices.
Fig. 2.
Comparison of the theoretical studentized t-distribution against filtered, down-sampled, and surrogate data using AR(1) data. (A) Compared to the theoretical studentized t-distribution (grey line), the distribution of t-values of filtered data (red line) exhibits greater variation, substantially increasing the chance of type 1 errors. Down-sampling the filtered data (orange line) tightens the distribution of t-values offering a closer approximation to the theoretical t-distribution, however the tails are still too wide. (B) Using surrogate data (blue bars) more closely approximates the distribution of down-sampled t-statistics (orange line) compared to the theoretical t-distribution (grey line).
Fig. 3.
Proposed framework for rsfMRI preprocessing and functional connectivity (FC) estimation.
This workflow explicitly incorporates key statistical corrections designed to minimize filtering-induced biases and correlation inflation. Following initial preprocessing—using only justified and clearly motivated filtering strategies—downsampling is performed whenever low-pass or bandpass filters are applied, preventing oversampling-induced artificial correlations. Surrogate datasets are generated ideally from the original, unfiltered data to accurately preserve underlying statistical (ARMA) properties. These surrogate data are then processed with identical filtering and downsampling procedures as the empirical data, creating robust statistical controls. Such matched surrogate data facilitate direct, statistically rigorous comparisons, thereby ensuring the reliability and validity of functional connectivity estimates. *By accounting for filtering and sampling biases, this pipeline significantly reduces preprocessing- driven artifacts and improves the robustness of rsfMRI analyses. Note: Standard preprocessing steps should still include controls for motion, physiological noise, and scanner artifacts. Fully documented scripts demonstrating practical implementation of this pipeline are available in the Supplementary Material (see Supplementary Methods, sections "Code for Table 1," "Code for Fig. 1," and "Code for Supplemental Tables S1 and S2").
Practical implementation: To facilitate immediate application of surrogate-based analyses, we have included fully documented Python scripts in the Supplementary Material. These scripts illustrate step-by- step instructions to: (1) export preprocessed BOLD signals (e.g., after filtering and downsampling) from standard neuroimaging toolkits (e.g., CONN, AFNI, FSL, or SPM), (2) generate and analyze surrogate datasets externally, and (3) re-import surrogate analysis results back into standard neuroimaging tools for subsequent visualization and statistical inference.
However, when analyzing a large number of experiments, a strong correlation within rsfMRI time series (or between rsfMRI and electrophysiological signals) may not necessarily indicate a true relationship, even after applying surrogate-based corrections and adjustment for multiple comparisons. As the number of experiments increases, the probability that at least one experiment will yield a surrogate-adjusted p-value passing the Bonferroni correction threshold approaches 100%, raising the risk of false positives.
To address the bias introduced by a large number of experiments, a potential solution is to treat the number of experiments with significant correlations as a statistic in itself. Specifically, for each experiment in the study, surrogate data based on the actual data must be generated. The count of experiments yielding significant correlations even after applying Bonferroni correction serves as the test statistic. This process should then be repeated multiple times (e.g., 100 iterations) to generate a null distribution of this test statistic. The newly created null distribution can then be used to evaluate whether the observed number of experiments with Bonferroni-corrected significant correlations is itself statistically significant. This approach introduces a second layer of statistical analysis, effectively mitigating the bias caused by the sheer number of experiments and ensuring the reliability of the study’s results.
The surrogate data approach outlined here is expected to produce unbiased results, provided it is properly implemented. By combining surrogate-based null distributions with robust multiple-comparison corrections (after adjusting sampling rate according to the encoded information), this method offers a reliable solution to address biases in rsfMRI data analysis.
3. Statistical limitations in diagnosis: implications for statistical power
Highlights:
While FC can be effective for population studies involving thousands of cases, it is unreliable for individual patient diagnosis. Machine learning holds promise for improving diagnostic power, but its clinical applicability is currently limited by preprocessing-induced biases, modest input signal correlations, and, in some architectures, a lack of mechanistic transparency. Recent advances in explainable AI have improved the interpretability of many ML models, but rsfMRI-based predictions still require rigorous statistical validation to ensure robustness.
The ultimate goal of rsfMRI-derived FC is to assist in diagnosing various diseases. However, as outlined in Section 2, standard statistical methods, hampered by issues such as cyclicity and auto-correlation, undermine the reliability of FC measures. A recent large-scale statistical study by Marek et al. (Marek et al., 2022) applied these conventional methods to extensive datasets and still reported only modest correlations between FC and behavioral phenotypes, underscoring the limitations inherent in current approaches. We extend this analysis to a diagnostic context by leveraging their results, obtained using a standard statistical framework, to evaluate the challenges of individual patient diagnosis. This approach illustrates how translating group-level data derived from standard analyses into reliable clinical tools remains a formidable challenge.
The reproducibility of rsfMRI data has been a subject of ongoing concern (Marek et al., 2022; Arbabshirani et al., 2014; Nee, 2019; Yarkoni et al., 2009). While reproducibility challenges are well recognized across neuroimaging, they are particularly pronounced in rsfMRI due to the inherent noisiness of resting-state signals and the impact of various confounding factors (Murphy et al., 2013). These reproducibility issues further compromise the reliability and validity of rsfMRI findings, thereby exacerbating the challenges of applying rsfMRI for individual clinical diagnosis. Addressing these issues is crucial not only for advancing rsfMRI research but also for developing robust, clinically applicable diagnostic tools.
Recent advances in large-scale multi-site studies have provided insights into the reproducibility of rsfMRI-derived FC across different populations and scanners. These efforts have shed light on the importance of methodological standardization and data sharing to improve the generalizability of rsfMRI findings. Collaborative initiatives, such as the Human Connectome Project, have played a pivotal role in promoting data transparency and fostering more robust and reproducible rsfMRI research (Van Essen et al., 2013).
In this context, we specifically focus on the diagnostic applicability of rsfMRI-derived FC when analyzed using standard statistical methods (Marek et al., 2022). While many studies claim potential clinical relevance for rsfMRI FC (Greicius et al., 2004; Corbetta, 2012; Siegel et al., 2024; Drysdale et al., 2017; Kaiser et al., 2015; Whitfield-Gabrieli and Ford, 2012), our analysis reveals that even with robust preprocessing and large sample sizes, the observed correlations are too modest to support reliable single-patient diagnosis. Note that since FC is a correlative measure, its applicability in a clinical setting should be approached with caution. As mentioned in the previous section, correlation-based measures make no assumptions on the causality between the observed variables and is subject to many biases, such as the effect of the sample size, auto-correlation, or residual noise (Hung et al., 2017).
Our analysis is based on a recent paper that analyzed three of the largest datasets of patients to quantify brain-wide association studies (BWAS) effect sizes and reproducibility as a function of sample size (Marek et al., 2022). They found that thousands of subjects are needed to establish statistically significant relationship between FC and cognitive or mental health phenotypes. While this insight underscores the need for substantial data collection efforts, it highlights the potential challenges of applying rsfMRI FC on an individual patient basis. The paper reported low correlation coefficients between rsfMRI FC and various behavioral metrics (the median was approximately 0.03 and 0.16 was the highest).
Let’s consider a scenario where a patient with known FC visits a psychiatrist who aims to incorporate FC into the diagnosis by associating FC with mental health phenotypes using trained data from consortium datasets. For the purpose of this discussion, we define a patient exhibiting a mental health phenotype greater than 0 as suffering from a specific health disorder. As an example, let’s assume the patient exhibits a strong FC of 0.7 between two brain structures deemed crucial for the diagnosis.
To predict the likelihood of making a correct diagnosis based on FC and mental health phenotypes, we first consider the Fisher z-scores of both variables, which follow a standard normal distribution. The correlation between the two Fisher z-scores will equal the slope of the best fit line (Ott and Longnecker, 2001). Additionally, the standard error of the regression between the two Fisher z-scores can be closely approximated (given a sufficiently high sample size) as the square root of one minus the correlation squared (Zar, 1999) (see Supplement, section: Derivation for Fisher’s z-transform and Regression Standard Error Approximation).
Now, with a positive correlation between the Fisher z-scores at best being 0.16, we predict that the average z-score of the mental health phenotype will be the hyperbolic arctangent of 0.7 times 0.16, which results in 0.1388. Utilizing the approximation of the standard error of the regression, we obtain a value of 0.9871 (see Supplement, section: Derivation for Fisher’s z-transform and Regression Standard Error Approximation). Since errors are assumed to be normally distributed, this implies that slightly over 44 % of our predicted mental health phenotype values fall below 0. Therefore, with a correlation of 0.16, a patient with an FC of 0.7 can only be diagnosed correctly at a rate of 56 %, which is not sufficiently high to aid in diagnosis. To achieve a correct diagnosis rate of 80 %, the patient would need to have an FC of at least 0.99 between the two brain regions.
Notably, these results were derived using a generous threshold of 0 for diagnosis, assuming that 50 % of the population would be suffering from the particular psychiatric disorder. In reality, a higher, more realistic threshold for diagnosis would further increase the FC value required for correct diagnosis. These findings underscore the importance of considering the strength of FC and its correlation with health phenotypes when using rsfMRI as a diagnostic tool after standard analysis of rsfMRI data. Achieving a high diagnostic accuracy using FC alone might necessitate strong and consistent FC values in the brain regions relevant to the specific mental health disorder.
To address the limitations of traditional statistical approaches in rsfMRI, there are high expectations for machine learning (ML) methods to improve diagnostic reliability. In particular, deep learning (DL) algorithms—including convolutional neural networks (CNNs) and recurrent neural networks (RNNs)—have shown promise in identifying complex, non-linear patterns in high-dimensional fMRI data (Smucny et al., 2022). However, despite their potential, DL-based diagnostic models have so far demonstrated only modest accuracy, with correct classification rates around 60 % in psychiatric disorders (Gallo et al., 2023; Wen et al., 2018).
A major limitation of DL approaches is their lack of interpretability, making it difficult to understand how predictions are generated. This “black box” nature poses significant challenges for clinical implementation, as clinicians require transparency in decision-making, particularly when communicating diagnoses to patients and satisfying medical regulatory standards. Without mechanistic insight into the FC changes underlying psychiatric and neurological disorders, deep learning models alone cannot provide sufficient justification for clinical decision-making (Chekroud et al., 2024).
However, it is important to acknowledge that recent developments in explainable artificial intelligence (XAI) have led to significant progress in improving the interpretability of machine learning models in neuroimaging. Methods such as saliency mapping, layer-wise relevance propagation, SHAP values, and attention-based architectures have been applied to fMRI and EEG data to elucidate decision-making features. Several studies (McClure et al., 2023; Garcia Santa Cruz et al., 2023; M. Liu et al., 2017; Zhang and Shen, 2012) have demonstrated that machine learning, when paired with robust preprocessing and transparent model design, can outperform traditional statistical methods in classification and regression tasks, particularly in well-controlled group-level comparisons. While challenges remain in clinical translation, especially for single-subject applications, these advances underscore that interpretability is an evolving technical property rather than a fixed limitation of machine learning itself. Importantly, these statistical concerns are not resolved by employing more sophisticated downstream analyses, including deep learning methods, since such approaches inherently depend upon accurately estimated functional connectivity measures derived during preprocessing. Recent examples of DL applications to fMRI data (McClure et al., 2023; Garcia Santa Cruz et al., 2023; M. Liu et al., 2017; Zhang and Shen, 2012) demonstrate significant potential but remain susceptible to underlying preprocessing-induced statistical biases highlighted here.
One potential solution is to combine DL methods with direct neurophysiological investigations to develop interpretable mechanistic models. For instance, in epilepsy research, integrating deep learning with mathematical models for causal inference from invasive recordings such as Stereo-EEG has been proposed as a promising approach to identifying clinically relevant biomarkers (Hashemi et al., 2023). Similarly, Zhang et al. (2022) developed a deep learning-based algorithm to detect epileptogenic high-frequency oscillations from intracranial EEG data, highlighting the potential of combining these approaches to enhance diagnostic accuracy.
However, while deep learning may improve classification performance in electrophysiological studies, its application to rsfMRI FC remains fundamentally constrained by the statistical limitations of FC itself. If the input data are already biased due to filtering artifacts or autocorrelation, applying even the most advanced deep learning algorithms will not resolve these underlying issues. Thus, proper statistical validation, such as surrogate data analysis, remains essential specifically for rsfMRI applications, ensuring that detected FC patterns are not statistical artifacts introduced by preprocessing choices. While deep learning may aid in hypothesis generation, it should be complemented by rigorous statistical testing before its outputs can be considered reliable for clinical use.
Another strategy for mitigating overfitting and controlling Type I error in rsfMRI-based classification is to implement empirical risk bounds. These techniques, drawn from statistical learning theory, provide guarantees that the model’s observed performance does not deviate excessively from its expected performance on unseen data. Górriz et al. (Górriz et al., 2019; Górriz et al., 2020) derived distribution-free upper bounds tailored for linear classifiers in neuroimaging applications with small sample sizes, using combinatorial geometry to analytically constrain classifier error. Their results demonstrate that, under certain conditions, the resubstitution error can offer competitive or even preferable estimates compared to traditional cross-validation. This form of theoretical control complements surrogate testing and downsampling by addressing the statistical reliability of model generalization and classifier robustness.
However, currently, our analysis of rsfMRI FC in association with mental health phenotypes reveals several caveats for its clinical applicability, particularly in psychiatry. While large-scale studies involving thousands of patients may yield statistically significant but relatively low correlations between rsfMRI FC and mental health phenotypes, these correlations cannot be directly utilized for the diagnosis of an individual patient, unless the patient exhibits extremely high FC values, which are not feasible in most cases. Thus, unlike research studies conducted on population datasets, the clinical utility of long-range rsfMRI and its trained models for the diagnosis of a single patient is limited. The challenge of relying on rsfMRI FC alone for diagnostic purposes stems from the modest correlations observed, which may not readily translate into meaningful insights for individual patient care.
The limitations identified in the clinical applicability of rsfMRI FC should not overshadow its potential as a research tool to study brain function and large-scale neural network alterations associated with mental health disorders, particularly, when a proper surrogate data analysis is implemented. Furthermore, there is potential for fMRI in combination with other modalities, such as structural MRI, spectroscopy, EEG, and MEG (Calhoun and Sui, 2016). These complementary modalities can provide additional insights into anatomical structures, biochemical processes, and real-time electrical activity, thereby enhancing the interpretation of rsfMRI data and mitigating some of its intrinsic limitations.
In summary, resting-state fMRI research still faces significant methodological and statistical challenges that must be addressed before achieving reliable clinical applications.
First, fundamental preprocessing artifacts and statistical biases undermine the reliability of FC estimates, directly affecting its utility in individual diagnoses. The widespread use of bandpass filtering (e.g., 0.01–0.1 Hz) without appropriate downsampling artificially inflates correlation values, leading to false positives that distort FC estimates. This filtering-induced bias cannot be fully corrected using standard multiple comparison adjustments nor by pre-whitening, which has been shown to be insufficient for removing autocorrelation in rsfMRI signals. Instead, adjusting the sampling rate to match the filtering choice and implementing surrogate data methods provide necessary safeguards against spurious FC estimates.
Second, the cyclic nature of resting-state hemodynamics creates accidental correlations that standard statistical methods fail to address. These biases systematically distort FC measurements and inflate statistical significance, leading to unreliable findings. As demonstrated in Section 2, filtering amplifies these issues rather than mitigating them, further confounding FC-based inferences. The impact of cyclicity extends beyond correlation-based analyses and must be accounted for when developing rsfMRI-based diagnostic models.
Finally, the limitations of rsfMRI FC become particularly evident when applied at the level of individual patient diagnosis. Large-scale studies have demonstrated that FC correlations with behavioral and cognitive measures are often modest and variable, making direct diagnostic use unreliable. This lack of robustness is likely due to the methodological flaws outlined in Section 2, including autocorrelation, filtering artifacts, and improper statistical controls. These statistical weaknesses propagate into machine learning and deep learning models trained on rsfMRI data, further reducing their reliability for clinical application. Since deep learning approaches typically rely on preprocessed FC features rather than raw fMRI signals, any preprocessing- induced biases, such as filtering artifacts or inflated correlations, are directly inherited by these models. Future research should focus on refining analytical methodologies and rigorously validating deep learning outputs using statistical safeguards, such as surrogate data analysis, to ensure that observed effects are not preprocessing artifacts.
By addressing these fundamental statistical challenges (correcting filtering biases, accounting for cyclicity, and ensuring proper statistical validation) rsfMRI research can move toward greater clinical reliability and reproducibility. Until these methodological limitations are resolved, FC-based approaches will remain challenging for individual patient diagnosis.
4. Additional confounds in rsfMRI
This section includes additional factors that can indirectly influence the results of statistical analysis in rsfMRI. In our previous analyses we focused on statistical issues arising from cyclicity, which is an inherent property related to the nature of the rsfMRI signal. Correlation bias due to cyclicity occurs even in the absence of any confounds. Therefore, our previous analyses assumed an ideal signal where these confounding factors were already addressed. The presence of confounds in the rsfMRI signal can enhance statistical challenges associated with cyclicity, while also negatively affecting the reproducibility and reliability of the results.
4.1. Effects of anesthesia, pain and stress on resting state neuronal activity and fMRI
Typically, local resting state activity of a majority of neurons is spontaneous and not synchronized during the awake state, in comparison with conditions such as anesthesia, epilepsy, pain, and stress (Hermans et al., 2011; Ploner et al., 2017; Flores et al., 2017; Aksenov et al., 2023; Doubovikov et al., 2023). Anesthesia produces two types of effects on vasomotion: it shifts its frequency towards lower values (Linsenmeier et al., 2016), and, if burst suppression is initiated, it is capable to induce response-like vasodilation. Each burst, which represents synchronous neuronal activity (Doubovikov et al., 2023), produces a hemodynamic response based on its amplitude, visible on fMRI (Sirmpilatze et al., 2022). These effects significantly increase the chances of interregional correlations, primarily associated with anesthesia effects. This introduces a statistical confound—burst suppression—driving correlation values, which could give a misleading impression of FC. For example, a recent study (Vedaei et al., 2022) reported that general anesthesia improved the reliability of rsfMRI metric measurements and shortened the optimized scan length in patients. Similarly, a study on rats (Becq et al., 2020) demonstrated that most brain areas were "active"—connected to at least one other brain area under anesthesia. However, it is crucial to differentiate "true" FC from anesthesia-induced changes, such as the natural decrease in the frequency of vasomotion and periods of burst suppression. This differentiation remains a challenging task, as anesthesia can simultaneously enhance apparent connectivity. On the other hand, if the level of anesthesia is too deep, it can result in prolonged periods of isoelectricity, where neurons lose control over vasomotion, leaving it dominated by very low-frequency components (around 1 cpm) across multiple brain areas. Similar to applying a stringent low-pass filter (see Section 2.3), anesthesia can enhance auto-correlative bias due to the abolition of the higher frequency component of the rsfMRI signal, which is always present in the awake state. Such conditions can further complicate rsfMRI analysis by eliminating neuronal-driven vasomotion and amplifying spontaneous vasomotion, necessitating careful consideration in interpreting connectivity metrics.
Epilepsy is another example where neuronal activity enters a synchronous or even hypersynchronous state in the absence of any external stimulation or task (Jiruska et al., 2013). In the US, 1.2 % of the population suffer from active or current epilepsy (Zack and Kobau, 2017). This statistic doesn’t include patients who may suffer from subclinical epileptic activity which is either not reported or only observed in combination with other pathologies. For example, 42 % of patients with Alzheimer’s disease have subclinical epileptic activity, which is significantly higher than general population (Vossel et al., 2016). Similar to burst suppression, epileptic activity induces response-like vasodilation for each burst. Any correlation observed between ROI’s located in the epileptic focus would be a reflection of similarly timed epileptic bursts, as opposed to actual resting state FC, representing an additional statistical confound.
Pain introduces stimulation (Zhang et al., 2018) and a subsequent avoidance neuronal response, which may not visibly manifest as movements but will produce strong neuronal activity which can spread across many brain regions.
Stress poses another confound to resting state recordings. Stressful stimuli activate the stress system (Godoy et al., 2018). Beyond the activation of the Sympathetic-Adreno-Medullar (SAM) axis and the Hypothalamus-Pituitary-Adrenal (HPA) axis, the complexity of the stress response, depending on the strength and duration, can reconfigure neuronal circuits across multiple brain regions (Hermans et al., 2011; Godoy et al., 2018). This reconfiguration of large-scale brain networks can be observed in fMRI recordings (Weldon et al., 2015) and obscures the studied effects. The stress system and its subsequent effects on fMRI recordings become a prevalent problem when using a mouse or rat model, especially when those animals are immobilized. Immobilization, even after habituation, should be used with great caution because the immobilization of rodents is one of the most reliable models to produce peptic ulcer due to stress (Pare, 1980).
Neuronal responses to pain or stress, visible in the gamma band of local field potential (LFP) or multi-unit activity (MUA), can create the false impression that vasomotion is entrained by gamma-band oscillations or MUA during rest (Zhang et al., 2018; Vandael et al., 2023). The longer pain or stress persists, the stronger the correlation between neuronal activity and vasomotion, further complicating rsfMRI analysis. Monitoring and excluding such activity is essential for robust interpretation.
4.2. Global signal regression
The global signal is commonly defined as the mean time course over all voxels in an fMRI scan (Zarahn et al., 1997). The rationale behind extracting the global signal is to capture nuisance components that may be present in all brain time courses (T.T. Liu et al., 2017). These nuisance sources include MRI system noise (Foerster et al., 2005; Power et al., 2015), slow physiological drift (Evans et al., 2015; Yan et al., 2009), motion related artifacts (Power et al., 2015; Hajnal et al., 1994), and fluctuations linked to cardiac and respiratory cycles (Wise et al., 2004; Shmueli et al., 2007; Chang et al., 2009; Windischberger et al., 2002; Berntson et al., 1993). Additionally, changes in vigilance and arousal states have been shown to influence the global signal (Wong et al., 2013; Chang et al., 2016; Falahpour et al., 2016).
The practice of treating the global signal as a nuisance variable and removing it from the data via regression is known as global signal regression (GSR). Initially introduced in task-based fMRI (Macey et al., 2004), GSR has also been applied to rsfMRI FC (Fox et al., 2009; He and Liu, 2012). However, its use in rsfMRI remains highly controversial (Murphy and Fox, 2017), primarily due to its tendency to introduce spurious anti-correlations (Murphy et al., 2009).
A key limitation of GSR is the lack of interpretability of the global signal, as it contains both neuronal and non-neuronal components (Murphy and Fox, 2017). Consequently, its removal may distort meaningful neural signals alongside unwanted noise. Similar to the concerns raised with bandpass filtering (see Section 2), the potential signal distortion caused by GSR must be properly justified and evaluated rather than applied as a default preprocessing step.
4.3. Motion correction artifacts in fMRI: implications for statistical analysis
Motion artifacts are a pervasive challenge in fMRI studies, arising from large subject movements during data acquisition (Liu, 2016; Ciric et al., 2018). These artifacts introduce significant noise into the BOLD signal, complicating the interpretation of FC and task-related activations. Head movements particularly can result in substantial spatiotemporal signal variability, leading to biases in statistical analyses. Motion-induced signal changes often mimic neuronal activity or inter-regional connectivity, creating spurious correlations that undermine the reliability of fMRI-based conclusions (Power et al., 2012; Satterthwaite et al., 2012).
From a statistical perspective, motion artifacts disproportionately affect high-frequency components of the fMRI signal. These artifacts can inflate correlation coefficients in FC analyses, as motion-related signal changes may overlap with true neurophysiological signals (Van Dijk et al., 2012). Furthermore, motion-induced fluctuations can mimic propagation across multiple regions, artificially increasing inter-regional connectivity metrics. Such spurious correlations are particularly problematic in resting-state fMRI, where the aim is to distinguish intrinsic connectivity patterns from artifacts caused by subject movement. These biases can lead to false positives in group-level comparisons and undermine the validity of findings in individual-level analyses. However, sufficiently large sample sizes may statistically suppress the impact of motion artifacts in group-level analyses, reducing their overall effect on aggregated results.
Motion correction algorithms, implemented in popular fMRI preprocessing pipelines like SPM, FSL, and AFNI, aim to mitigate these effects by realigning images to a reference volume (Friston et al., 1996). However, residual motion artifacts often persist, especially in datasets with substantial head motion. The interplay between voxel resolution and noise, can also affect data quality (Triantafyllou et al., 2005). Advanced methods, such as ICA-based artifact removal (Pruim et al., 2015) or frame-wise displacement metrics, allow for the exclusion of motion-affected volumes. While these approaches improve data quality, they may introduce additional biases, such as the over-scrubbing of volumes in subjects with higher motion, potentially skewing group-level comparisons (Power et al., 2014).
The statistical implications of motion correction are particularly evident in studies involving pediatric or clinical populations, where motion is more pronounced (Satterthwaite et al., 2013). Higher motion rates in these groups can lead to systematic biases in connectivity measures, necessitating careful consideration of confounding variables. Researchers must also account for motion-related variability in subsequent statistical tests, incorporating motion regressors or using surrogate data techniques to ensure robust hypothesis testing (Bright and Murphy, 2013). For a comprehensive overview of protocols designed to mitigate motion-related artifacts, see (Ciric et al., 2018). Ultimately, while motion correction techniques significantly reduce the impact of artifacts, they cannot completely eliminate motion-induced biases. This limitation underscores the need for improved preprocessing methods and robust statistical frameworks in fMRI analysis, which should incorporate strategies such as sufficient repetitions or larger sample sizes to mitigate the residual effects of motion.
4.4. Small movements as sporadic stimulation in resting state
The presence of small movements, such as eye movements, whisking, and postural adjustments, introduces a critical consideration in the interpretation of rsfMRI signals. These movements can induce neuronal activation and subsequent hemodynamic responses, complicating the distinction between intrinsic resting-state activity and stimulus-driven responses. In animal models, pain or discomfort often elicits such movements as expressions of avoidance behavior. In humans, small movements are typically due to the inability to remain completely still, a factor that varies across individuals.
Small movements should be distinguished from motion-related artifacts. Small movements induce stimulation that triggers neuronal responses and subsequent hemodynamic activity without directly introducing motion-related noise into the signal. Conversely, motion-related artifacts add noise to the signal due to physical displacement of the subject (Liu, 2016; Ciric et al., 2018). Previous studies have attempted to quantify and correct for the impact of small movements on resting-state signals, but the topic remains contentious. For example, researchers have proposed detection and correction methods for small “fidgeting” movements (Drew, 2019). Additionally, it has been suggested that these small movements may contribute to the origin of the rsfMRI signal itself (Drew et al., 2020). This raises fundamental questions about the underlying mechanisms and definitions of rsfMRI, particularly whether it reflects genuine neurovascular resting-state interactions or a sequence of events tied to neuronal responses driven by sporadic stimulation or task-like activity, where stress, pain, or discomfort increases the frequency of such events.
If small movements are considered an inherent part of rsfMRI, developing methods to control or standardize their incidence may enhance reproducibility. However, the random nature of the duration, location, and timing of hemodynamic responses associated with these movements complicates their distinction from random stimulus sequence fMRI (Clark et al., 1998), although in random stimulus sequence fMRI, the locations of responses are predefined.
Alternatively, if small movements are treated as confounding response-like noise, efforts should focus on mitigating their influence by employing identifiable markers, such as neuronal activity measures or video monitoring, to clean rsfMRI signals. Failure to account for small movements raises significant concerns about the reproducibility and reliability of findings, particularly in dynamic FC analyses. Random events, such as sporadic small movements, introduce additional uncertainty into the interpretation of dynamic FC. Similarly, burst suppression, which can randomly appear and disappear under general anesthesia, introduces comparable confounds by generating synchronized neuronal activity unrelated to resting-state connectivity.
In conclusion, small movements and other random events represent distinct yet significant challenges for rsfMRI analysis, both requiring careful differentiation from intrinsic resting-state signals. Addressing these issues is critical for improving the reliability, reproducibility, and validity of rsfMRI findings, particularly in studies investigating dynamic FC
4.5. Operational definition of rsfMRI
Despite its apparent simplicity, resting-state fMRI lacks a strict definition, making it vulnerable to confounds that reduce its reliability and reproducibility. To minimize artifacts and improve methodological consistency, a clearer definition is needed. Historically, rsfMRI definitions fall into three major categories, each with limitations. We propose a fourth category that explicitly accounts for physiological and pathological states influencing FC.
Task-embedded rsfMRI: rsfMRI can include tasks and perhaps even stimulation as long as it occurs in a random sequence (Snyder and Raichle, 2012; Fransson, 2006). However, this approach blurs the boundary between rsfMRI and random stimulus sequence fMRI which we mentioned previously and assumes involvements of random events which diminishes the replicability of rsfMRI.
Absence of external stimulation: rsfMRI represents the state of the brain in the absence of stimulation outside of the brain (Northoff et al., 2010). This definition does not account for internally initiated tasks like thinking or even voluntary and non-voluntary movements which can occur without an external trigger (Greicius et al., 2003).
Absence of stimulus and task: The strictest definition of rsfMRI requires the absence of both external stimuli and internal cognitive tasks (Lv et al., 2018). This definition most clearly represents resting state, however, it does not take into account changed brain states, like stress, epilepsy, or effects of anesthetics at the level of burst-suppression, where the majority of neurons are synchronized even without external stimulus or task, which can generate structured low-frequency neuronal activity independent of spontaneous FC.
Exclusion of pathological synchronization: We propose a refined definition in which rsfMRI must be free from external stimulation, task-related activity, and intrinsic pathological states. Epilepsy, burst suppression, and acute stress all induce strong neuronal synchronization that activates neurovascular responses, contaminating FC estimates. These states introduce a structured BOLD signal resembling FC, but they do not reflect baseline intrinsic network dynamics.
In the resting state, significant deviations in hemodynamic function or baseline oxygen consumption due to strong synchronization of neuronal networks are generally unexpected (Karkan et al., 1999), as the resting state is fundamentally defined by the absence of stimulation (Northoff et al., 2010; Lv et al., 2018). However, persistent, localized increases in hemodynamics or oxygen consumption suggest pathological alterations rather than spontaneous FC. In patients with chronic epileptic activity, additional precautions—such as EEG-informed fMRI, detection of interictal discharges, or isolating periods of relative quiescence—may be necessary to minimize the impact of pathological synchronization on FC estimates. This distinction is critical because, (a) FC measurements in epilepsy, burst suppression, or stress do not reflect intrinsic resting-state networks. (b) Spontaneous network activity must be distinguished from pathological states generating hemodynamic responses. (c) rsfMRI should exclude intrinsic neuronal synchronizations that distort FC estimates, requiring stricter inclusion criteria.
By excluding task-evoked, internally generated, and pathological neural events, this refined definition ensures that rsfMRI analyses are applied only to conditions that truly reflect spontaneous FC. This approach strengthens the reliability of rsfMRI as a measure of intrinsic brain activity and minimizes spurious connectivity estimates arising from non-resting-state influences.
Supplementary Material
Supplementary material associated with this article can be found, in the online version, at doi:10.1016/j.neuroimage.2025.121334.
Acknowledgment
R01 GM112715 and R01 NS107383.
Footnotes
CRediT authorship contribution statement
Evan D. Doubovikov: Writing – review & editing, Writing – original draft, Methodology, Investigation, Formal analysis. Daniil P. Aksenov: Writing – review & editing, Writing – original draft, Supervision, Funding acquisition, Conceptualization, Methodology, Investigation.
Declaration of competing interest
The authors declare that they have no known competing financial interests or personal relationships that could have appeared to influence the work reported in this paper.
Data availability
The code supporting this work is provided in the Supplement. Emprical data were obtained from the Human Connectome Project (HCP) dataset, and used under IRB approval.
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Data Availability Statement
The code supporting this work is provided in the Supplement. Emprical data were obtained from the Human Connectome Project (HCP) dataset, and used under IRB approval.