The objective of this meta-analysis was to assess whether to mindfulness meditation concurrent with consumer-grade neurofeedback had beneficial effects compared with control conditions. Mindfulness meditation is known to have benefits for psychological distress, cognitive functioning, and physiological health [3,67-69], and we assessed whether mbNF had significantly more positive outcomes in these domains. Separately from outcomes, we also assessed effects of mindfulness on process variables like state and trait mindfulness, as well as whether participants can modulate brain signals through mbNF. We preregistered this meta-analysis before examination of the data, on OSF Registries [70]. All deviations can be found in Multimedia Appendix 1.

Randomized studies that used cgNF (Figure 1 [47]) concurrently with mindfulness meditation and had a control condition were included (Textbox 2 and Table 1).

We extracted a comprehensive set of outcomes from the methods section of the included papers and addressed any missing statistics using reporting bias sensitivity analyses (refer to the Analysis section). We collected psychological distress outcomes, including anxiety, depression, fatigue, as well as positive affect, where decreases reflect decreased distress, for example, decreased anxiety or increased positive affect. We collected cognitive outcomes, exclusively behavioral tasks like vigilance and complex reaction time where improvements reflect better cognitive functioning, for example, increased accuracy, or reduced reaction times. We also collected physiological health outcomes including heart rate variability, where increases reflected better health after confirming that these matched hypotheses of the studies. Process variables also were extracted. Specifically, state and trait mindfulness were collected, consisting of established questionnaires like the Five-Facet Mindfulness Questionnaire [85], as well as any study-specific questionnaires that assessed mindfulness as present-moment attention or acceptance. Finally, brain target measures as reported by the consumer-grade devices to assess whether participants were able to successfully modulate brain targets were extracted.

A search of PubMed, Web of Science, PsycInfo, and Scopus, was completed on November 11, 2023. Databases were identified based on previous mindfulness systematic reviews and meta-analyses [86,87]. Search terms were “(mindfulness OR meditation) AND (neurofeedback OR neural feedback OR neuro feedback).” We additionally searched reference sections of included papers.

All studies were first screened for duplicate publications. Next, all abstracts were screened, including studies based on 2 main criteria: an empirical study (examples of excluded articles were review papers and protocol papers) and content relevance (based on above stated eligibility criteria). Then remaining studies were screened by reviewing the methods section and full paper to further evaluate the presence of inclusion criteria. Determination of inclusion was established in cases of disagreement by consulting with the first author.

A coding manual was developed by the first author to guide the extraction of study descriptive and effect size data. Extraction of these data was conducted by the first author and confirmed independently by authors (ZB, KDG, and NK). Coding disagreements were discussed by the team.

We extracted the following descriptive variables: duration of neurofeedback in minutes and training weeks, participants in mbNF and control conditions (after dropout), control condition type, mbNF device used, delivery modality, type of meditation, age, percentage female (using reported sex), whether or not it was a clinical population, and outcome types. We reported these variables separately for within-participant and between-participant designs (refer to Tables 1 and 2). In the case of multiple intervention groups or control groups, we combined the groups (and pooled their means and SDs). A minority of studies reported overall N but did not report final group numbers, in which case we imputed equivalent group sizes, and coded it as additional risk of bias.

For between-participant designs, we primarily calculated Becker’s del for effect sizes, which is the Cohen d for the mbNF group minus the Cohen d for the control group [93]. This provides a simple measure of the degree of differential change between the groups. In cases of incomplete reporting, we converted t tests or partial eta-squared to Cohen d. All effect sizes were converted using Hedges g correction, as many sample sizes were small. Variances of effect sizes were calculated using standard methods [93,94]. For within-participant designs, we conducted simple mean differences between the mbNF and control condition, converting using Hedges g correction.

Bias assessment was conducted on the RCTs included in the review, following PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) guidelines [95]. RCTs were rated using the risk of bias (ROB)-2 [96]. Two authors (IT and either ZB, KDG, or NY) independently rated the risk across several domains, including (1) randomization, (2) blinding, (3) objective measurement of outcomes, (4) attrition, and (5) reporting bias. This estimated risk in each domain was then compared between raters. Any disagreements were discussed and resolved (95% of ratings were identical). After inter-rater agreement was reached, studies were classified as having low, some concerns, or high risk of bias. Methods for quantifying study quality are detailed in Multimedia Appendix 1.

A PRISMA flow diagram is shown in Figure 2 (PRISMA checklist provided in Multimedia Appendix 2). A total of 16 RCTs were identified, encompassing 763 unique participants, as well as 5 within-participant randomized studies, encompassing 157 participants. Average sample size was 47.68 participants and 31.2 participants, respectively. The average age was 25.69 (SD 10.01) years and 26.12 (SD 9.99) years, respectively. Three RCTs involved children [66] or adolescents [98,99]. The average proportion female was 66.19% and 47.83%, respectively. Sociodemographic variables were not consistently reported. Four RCTs involved clinical samples (eg, obsessive compulsive disorder [80]), and 2 inductions involved individuals with intellectual disability [89,90]. Most studies used the Muse neurofeedback system (11/16 interventions and 4/5 inductions). The predominant meditation type was focused attention on the breath. Control conditions for studies were primarily active, consisting of mindfulness apps for RCTs (11/16), and short mindfulness meditations for within-participant designs. Passive controls (3 studies) consisted of waitlist or treatment-as-usual. Of the 16 RCTs, 7 were conducted by the same research group in Italy [73,78]. Two of the within-participant randomized studies had extremely small sample sizes (n<10). Four studies were preregistered. Full descriptions may be found in Tables 1 and 2.

The greatest concern in the RCTs was blinding (Figure 3 and Figure S1 in Multimedia Appendix 1). One study had a biofeedback control condition [82], and no studies had sham neurofeedback. There were also concerns with inadequate reporting of randomization and attrition. We address reporting bias in sensitivity analyses.

Effects for psychological distress were significant across a range of reporting bias corrections (g=–0.29 to –0.16, P<.05; Tables 3 and 4, Table S2 in Multimedia Appendix 1, and Figure 4). Heterogeneity was low after removing one outlier (I²<25%). Effects for cognitive function were sensitive to reporting bias, without correction the omnibus effect was significant (g=0.31, P=.04), but when correcting the effects were not significant (moderate g=0.20, strict g=0.07, P>.10; Tables 3 and 4 and Table S2 in Multimedia Appendix 1). Heterogeneity was moderate for cognitive outcomes (50%>I²>25%). Effects for physiological health, and mindfulness, were not significant (P>.10), and heterogeneity for physiology was high (I² >75%), even though the measures narrowly focused on heart rate and heart rate variability. Figure 5 presents the omnibus effect sizes for comparison. Results were similar when examining only studies with active controls (Table S3 in Multimedia Appendix 1). In summary, there was limited evidence for decreased psychological distress, but no identified improvements in cognitive function, physiological health, or mindfulness.

There were not sufficient studies to detect whether training increased the brain target scores. However, we conducted an exploratory analysis with the 3 RCTs that reported brain target scores and found no significant effect (g=–0.01; P=.95; 95% CI –0.39 to 0.36; I²=23.18; tau=0.16). We conducted an exploratory analysis on single-arm effects (no controls), which showed increased brain target scores (Multimedia Appendix 1).

We had sufficient studies to analyze whether mindfulness was higher during neurofeedback than during control conditions (k=4, g=0.14) and whether the brain target was modulated more during neurofeedback than during control (k=5, g=0.12; Table 5 and Figure S5 in Multimedia Appendix 1). Neither effect was significant (P>.15). There was no indication of reporting bias.

We largely did not find significant moderation effects for clinical population, age, percentage female, quality, or neurofeedback duration (Tables S4 and S5 in Multimedia Appendix 1). Physiological effects correlated negatively with overall sample size (B=–0.02, P=.02) such that stronger effects were observed in smaller samples.

For RCT studies, there was no indication of publication bias either through trim-and-fill or through selection models (Table S3 in Multimedia Appendix 1). Selection model regressions minimally changed omnibus estimates, except for physiological health, in which the effect size reversed from g=0.13 to g=–0.13, but neither was significant.

For within-participant studies, trim-and-fill detected low sample size studies with high effect sizes (Table S3 in Multimedia Appendix 1) and accordingly filled in studies on the left of the distribution, resulting in decreased gs that remained nonsignificant (Brain target g=0.01, Mindfulness g=0.06). This assessment should be qualified as one of the studies was a thesis, and not a publication. Selection models failed due to lack of significant P values.

Only 2 of the 21 studies evaluated monitored for adverse events, an important measure of the reliability and safety of an intervention. Neither reported any adverse effects.

There is increasing interest in technology-supported mindfulness, for promoting scalability, facilitating beginner practice, and increasing motivation and adherence. Here we examined cgNF for supporting mindfulness practice (mbNF). cgNF devices provide metrics of brain function to the user, putatively allowing them to optimize their brain and psychological states. We meta-analytically examined the effectiveness of mbNF in improving psychological and cognitive functioning, and physiological health as well as modulating state mindfulness and brain targets. Included studies consisted of 16 RCT training studies and 5 within-participant randomized studies. There is some evidence that mbNF may reduce psychological distress compared to control conditions, although the effect is small. Improvements in cognitive function were not robust to reporting bias correction, and effects on physiological health were likewise insignificant. There was no evidence for improvements in trait or state mindfulness, which are process measures of the effectiveness of a mindfulness intervention. Likewise, there is not conclusive evidence that participants can learn to modulate brain targets (eg, Muse “Calm” scores). We largely did not find significant moderation effects for clinical population, age, percentage female, study quality, or neurofeedback duration.

Our main finding was the small positive effect of mbNF (g=–0.29) on psychological distress, as measured by questionnaires measuring mood, anxiety, posttraumatic stress disorder symptoms, etc. This effect was observed above and beyond control interventions, including mobile meditation apps, although when conducting strict reporting bias correction, the effect shrank to g=–0.16. Benefits on stress and distress have been observed in previous reviews of mindfulness and technologically supported mindfulness [9,60,86]. There is little theoretical work on why neurofeedback may benefit mindfulness practice, but mechanisms in the neurofeedback literature generally fall into 2 categories. One, given the correct brain target, neurofeedback may actually lead to facilitated learning and self-regulation [34,35]. For example, in the context of laboratory-based neurofeedback, it is suggested that learning to regulate the default-mode network may lead to enduring changes in self-awareness, alleviating deleterious cycles of self-criticism [105]. Outside of the laboratory, it is less clear what exactly consumer-grade devices target in terms of brain mechanisms, and thus why they should alter psychological states [52]. We did not find evidence that cgNF improves mindfulness nor lead to changes in brain targets more than control conditions. This lack of mechanistic evidence makes it difficult to conclude that mbNF is alleviating psychological distress through brain modulation.

A second, more plausible mechanism is a specific placebo effect called “neurosuggestion” [106]. Western societies place a strong emphasis on biological determinants of the mind, and there is widespread trust and enthusiasm for technology and neuroscience. Meditating with cgNF may lead to enhanced motivation, feelings of self-efficacy, and expectations of benefits [107,108]. It is possible that this led to larger decreases in psychological distress compared with control conditions (which were typically potentially less motivating app trainings). The best way to rule out these explanations is through sham-controlled neurofeedback, where participants in the control condition also wear consumer-grade devices but receive “sham” neurofeedback [109]. In this design, the control participants would also experience “neurosuggestion,” and any differential effects must be related to the targeted brain changes. Even in laboratory-based studies, this evidentiary standard is rare (an exception is a sham-controlled RCT that found mbNF participants increased theta oscillations) [13,110]. None of the included consumer-grade studies in the present review used sham controls. One possible approach could be yoked sham, where control participants receive neurofeedback stimuli from another participant (and thus not associated with their own psychological or brain states). Sham controls are fundamental to establishing the efficacy of mbNF.

Effects may have been obscured because of limited power. In general, sample sizes were small (N<50). There was insufficient reporting to investigate the role of intervention fidelity on effects, including differences in device calibration, participant engagement, and adherence. Likewise, our preregistered moderators did not significantly relate to effect sizes, perhaps due to the lack of overall effects, or due to small samples. Per-protocol or dosage analyses could show that some participants experience greater benefits. Relatedly, none of the studies reviewed here extended longer than 8 weeks. An open-label study of Muse over 90 days found positive outcomes, good adherence and 71% of participants wanted to continue using Muse after the period ended [111]. Long-term effects of neurofeedback are unclear, and adverse events are insufficiently monitored in the field. Finally, some of our methods, while standard for meta-analysis, may have obscured effects. To correct for reporting bias, we first contacted authors, and then imputed zeros for mean effects in case of no response. There may have been nonsignificant but trending effects for these measures. We did not find evidence of publication bias, which is present in other biofeedback fields [112].

Limited efficacy of mbNF may arise from technological limitations. First, cgNF relies on dry electrodes on the scalp, which limits signal quality [113]. Signal may be contaminated by muscle movement in many cases and limited by narrow temporal windows of measurement [52]. Second, even given high fidelity measures of underlying brain signals (eg, alpha or beta power), these signals are not straightforward to map to psychological processes like attention [114,115]. Third, there may be serious variability between individuals in these mappings. For example, mind-wandering episodes are predictable within-individuals using whole-brain fMRI measures but the measures show extensive spatial variability between individuals [116].

To improve the efficacy of mbNF, one approach is to conduct more laboratory-based studies on mechanisms, including multimodal fusion studies where different imaging modalities are combined to assess common signatures of psychological processes. Another approach may be more extensive data collection and algorithm development by device companies. In the face of great individual variability, it may be useful to more extensively calibrate devices (“personalize”) to users before meditation sessions. Currently, users are given short calibration sessions of variable content before meditation, and one assumes that brain signals during calibration are baselines for the meditation session (eg, the goal is to reduce alpha compared to baseline [56]). There is no participant input in the calibration, and calibration procedures are highly variable across devices. If participants could indicate when they feel calmer or more focused, the devices could learn from their responses. In summary, more neuroscientific research on devices may lead to more effective mbNF, and this does not necessarily entail expensive fMRI studies.

A broader challenge is that mbNF assumes that some degree of monitoring during meditation may facilitate mindfulness. Feedback may actually be distracting in some cases [13]. Breath meditation typically emphasizes paying fine attention to the details of the breath and the sensations in various body parts. When attention wanders, one may lose track of the motion of the breath. Or one’s attention may become less precise and the details of the breath become harder to track. Meditation involves learning to notice these changes and develop insight into your mind. If the practitioner is paying attention to an auditory feedback signal instead, they may lose this awareness, and more importantly, lose out on the learning process of watching awareness fluctuate. It may be the case that open monitoring or “mental noting” [105], which allows for attention to shift between the stimulus, sensations, thoughts, etc, is more amenable (we were unable to examine moderation by meditation practice type in the current review). Furthermore, “intermittent” neurofeedback may facilitate awareness and insight without distractions [117]. This is speculative, and more research on qualitative experiences of neurofeedback (especially with advanced practitioners) is necessary. In addition, clear and thorough monitoring of adverse events is recommended.

The present meta-analysis of mindfulness-based neurofeedback finds evidence for modest decreases in psychological distress compared to controls. This effect may be placebo-related. There is little conclusive evidence for mechanistic engagement, nor improvements in cognition, mindfulness, nor physiological health. Placebo effects of neurofeedback should be taken seriously, as placebo is increasingly considered a meaningful treatment option for some individuals. In terms of treatments, cgNF is relatively inexpensive and accessible, devices are available online for US $100-$200 whereas MBSR courses or therapy or fMRI neurofeedback cost thousands of dollars. However, there are concerns about the commodification of mindfulness which originated as a spiritual practice [118].

Ultimately neurofeedback, biofeedback, and neuromodulation as technological supports for meditation may be constrained by the limits of noninvasive measurement, and the difficulty of linking such limited measures to mental states in a generalizable way. Of course, other forms of technology-supported mindfulness may be more powerful. For example, virtual reality and video games provide immersion, enhance mindful states and may reach people who are not interested in formal practice [9,10,119,120]. Mindfulness apps provide accessibility and customization for specific groups of individuals [121]. However, we should not overlook the significant role that teachers and therapists play in the success of standard mindfulness interventions [66,122-125], and more broadly, the key role of the therapeutic alliance on mental health outcomes even within technology-based treatments [126-129]. Given the escalating mental health crisis, it is imperative for practitioners to thoughtfully integrate evidence-based behavioral interventions with emerging technologies, while maintaining a rigorous focus on understanding which approaches work best for specific populations and the underlying mechanisms that drive their effectiveness.