Mindfulness‐based psychological interventions for improving mental well‐being in medical students and junior doctors

Praba Sekhar; Qiao Xin Tee; Gizem Ashraf; Darren Trinh; Jonathan Shachar; Alice Jiang; Jack Hewitt; Sally Green; Tari Turner

doi:10.1002/14651858.CD013740.pub2

. 2021 Dec 10;2021(12):CD013740. doi: 10.1002/14651858.CD013740.pub2

Mindfulness‐based psychological interventions for improving mental well‐being in medical students and junior doctors

Praba Sekhar ^1,^✉, Qiao Xin Tee ¹, Gizem Ashraf ¹, Darren Trinh ¹, Jonathan Shachar ¹, Alice Jiang ¹, Jack Hewitt ¹, Sally Green ¹, Tari Turner ¹

Editor: Cochrane Common Mental Disorders Group

PMCID: PMC8664003 PMID: 34890044

Abstract

Background

Mindfulness interventions are increasingly popular as an approach to improve mental well‐being. To date, no Cochrane Review examines the effectiveness of mindfulness in medical students and junior doctors. Thus, questions remain regarding the efficacy of mindfulness interventions as a preventative mechanism in this population, which is at high risk for poor mental health.

Objectives

To assess the effects of psychological interventions with a primary focus on mindfulness on the mental well‐being and academic performance of medical students and junior doctors.

Search methods

We searched the Cochrane Central Register of Controlled Trials (CENTRAL), MEDLINE, Embase and five other databases (to October 2021) and conducted grey literature searches.

Selection criteria

We included randomised controlled trials of mindfulness that involved medical students of any year level and junior doctors in postgraduate years one, two or three. We included any psychological intervention with a primary focus on teaching the fundamentals of mindfulness as a preventative intervention. Our primary outcomes were anxiety and depression, and our secondary outcomes included stress, burnout, academic performance, suicidal ideation and quality of life.

Data collection and analysis

We used standard methods as recommended by Cochrane, including Cochrane's risk of bias 2 tool (RoB2).

Main results

We included 10 studies involving 731 participants in quantitative analysis.

Compared with waiting‐list control or no intervention, mindfulness interventions did not result in a substantial difference immediately post‐intervention for anxiety (standardised mean difference (SMD) 0.09, 95% CI ‐0.33 to 0.52; P = 0.67, I²= 57%; 4 studies, 255 participants; very low‐certainty evidence). Converting the SMD back to the Depression, Anxiety and Stress Scale 21‐item self‐report questionnaire (DASS‐21) showed an estimated effect size which is unlikely to be clinically important. Similarly, there was no substantial difference immediately post‐intervention for depression (SMD 0.06, 95% CI ‐0.19 to 0.31; P = 0.62, I² = 0%; 4 studies, 250 participants; low‐certainty evidence). Converting the SMD back to DASS‐21 showed an estimated effect size which is unlikely to be clinically important. No studies reported longer‐term assessment of the impact of mindfulness interventions on these outcomes.

For the secondary outcomes, the meta‐analysis showed a small, substantial difference immediately post‐intervention for stress, favouring the mindfulness intervention (SMD ‐0.36, 95% CI ‐0.60 to ‐0.13; P < 0.05, I²= 33%; 8 studies, 474 participants; low‐certainty evidence); however, this difference is unlikely to be clinically important. The meta‐analysis found no substantial difference immediately post‐intervention for burnout (SMD ‐0.42, 95% CI ‐0.84 to 0.00; P = 0.05, I² = 0%; 3 studies, 91 participants; very low‐certainty evidence). The meta‐analysis found a small, substantial difference immediately post‐intervention for academic performance (SMD ‐0.60, 95% CI ‐1.05 to ‐0.14; P < 0.05, I² = 0%; 2 studies, 79 participants; very low‐certainty evidence); however, this difference is unlikely to be clinically important. Lastly, there was no substantial difference immediately post‐intervention for quality of life (mean difference (MD) 0.02, 95% CI ‐0.28 to 0.32; 1 study, 167 participants; low‐certainty evidence). There were no data available for three pre‐specified outcomes of this review: deliberate self‐harm, suicidal ideation and suicidal behaviour.

We assessed the certainty of evidence to range from low to very low across all outcomes. Across most outcomes, we most frequently judged the risk of bias as having 'some concerns'. There were no studies with a low risk of bias across all domains.

Authors' conclusions

The effectiveness of mindfulness in our target population remains unconfirmed. There have been relatively few studies of mindfulness interventions for junior doctors and medical students. The available studies are small, and we have some concerns about their risk of bias. Thus, there is not much evidence on which to draw conclusions on effects of mindfulness interventions in this population. There was no evidence to determine the effects of mindfulness in the long term.

Plain language summary

Mindfulness for improving mental well‐being in medical students and junior doctors

Why is this review important?

The medical profession is recognised for its challenging and demanding nature. Medical students and junior doctors have been identified as having increased personal and professional stressors during their years of training. As a result, they face increased strain on their mental well‐being. It is important that this group is supported in their mental well‐being to ensure an overall balance in health, as well as to aid their responsibilities of patient care and patient safety. Furthermore, medical students and junior doctors are often time‐poor. Therefore, it is important to establish whether mindfulness is an effective intervention which justifies its time commitment. There are no previous Cochrane Reviews examining mindfulness in our target population.

Who will be interested in this review?

Medical students and junior doctors; other medical professionals at different levels of training and expertise; and institutions such as universities and hospitals involved in the education and training of medical students.

What question does this review aim to answer?

What effects do mindfulness‐based psychological interventions have on the mental well‐being of medical students and junior doctors?

Which studies were included in this review?

We searched databases to find all studies of mindfulness in medical students and junior doctors published up to October 2021. In order to be included in this review, studies had to be randomised controlled trials (a type of study in which participants are assigned to groups using a random method). Studies needed to include medical students from any year level or junior doctors in postgraduate years one, two or three. We did not exclude any studies based on participants' age, nationality or pre‐existing health conditions. We included 10 studies with a total of 731 participants in the analysis.

What does the evidence from the review tell us?

Overall, we did not identify any evidence of an effect of mindfulness‐based interventions on anxiety or depression symptoms. However, mindfulness‐based interventions appeared to have a small positive effect on stress and a borderline positive effect on burnout. We were unable to report if mindfulness‐based interventions had any effect on deliberate self‐harm, suicidal ideation or suicidal behaviour as no studies examined these outcomes. Lastly, as many studies lacked longer‐term follow‐up of participants, it is not possible to comment on the long‐term effects of mindfulness in medical students and junior doctors.

We rated the overall certainty of evidence as 'low' or 'very low'.

What should happen next?

While there were no strong positive findings from the review, some results regarding mindfulness and stress outcomes suggest that there needs to be further research into mindfulness. Any future research should be rigorously designed, and ideally, include assessments of the longer‐term impact of mindfulness.

Summary of findings

Summary of findings 1. Mindfulness compared with no treatment or waiting list for improving mental well‐being.

Outcome	Anticipated absolute effects (95% CI¹)		No. of participants (studies)	Certainty of the evidence (GRADE)	Comments
	Assumed Risk	Corresponding Risk
	No mindfulness	Mindfulness
Anxiety assessed with 3 different questionnaires Follow‐up: immediately post‐intervention to 8 weeks	The anxiety score in the intervention groups was on average 0.09 SDs (0.33 lower to 0.52 higher) higher than in the control groups.		255 (4 RCTs)	Very low^a,c,d,e	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Converting the SMD back to DASS‐21 gives an estimated effect size of 0.31 units on the DASS‐21 scale, and a 95% CI of ‐1.14 to 1.80. Given this is less than 2 units on the DASS‐21 scale which ranges from 0 to 63 for anxiety, this is unlikely to be clinically important.
Depression assessed with 3 different questionnaires Follow‐up: 4 weeks to 3.5 months	The depression score in the intervention groups was on average 0.06 SDs (0.19 lower to 0.31 higher) higher than in the control groups.		250 (4 RCTs)	Low^a,d,e	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Converting the SMD back to DASS‐21 gives an estimated effect size of ‐0.11 units on the DASS‐21 scale, and a 95% CI of ‐0.35 to 0.56. Given this is less than 2 units on the DASS‐21 scale which ranges from 0 to 63 for depression, this is unlikely to be clinically important.
Stress (immediately post‐intervention) assessed with 2 different questionnaires Follow‐up: immediately post‐intervention to 8 weeks	The post‐intervention stress score in the intervention groups was on average 0.36 SDs (0.6 lower to 0.13 lower) lower than in the control groups.		474 (8 RCTs)	Low^b,d,e	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Converting the SMD back to DASS‐21 gives an estimated effect size of ‐0.74 units on the DASS 21 scale, and a 95% CI of ‐1.23 to ‐0.27. Given this is less than 2 units on the DASS‐21 scale which ranges from 0 to 63 for stress, this is unlikely to be clinically important.
Stress (later time points) assessed with 1 questionnaire Follow‐up: 6 to 12 months	The longer‐term stress score in the intervention groups was on average 0.43 SDs (0.69 lower to 0.17 lower) lower than in the control groups.		233 (4 RCTs)	Low^b,d,e	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Converting the SMD back to the Perceived Stress Scale (PSS), gives an estimated effect size of ‐1.04 units on the PSS, and a 95% CI of ‐1.66 to ‐0.41. Given this is less than 1 unit on the PSS, which ranges from 0 to 40, this is unlikely to be clinically important.
Burnout assessed with 2 different questionnaires Follow‐up: immediately post‐intervention to 10 weeks	The burnout score in the intervention groups was on average 0.42 SDs (0.84 lower to 0 higher) lower than in the control groups.		91 (3 RCTs)	Very low^b,d,e,f	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Converting the SMD back to the Copenhagen Burnout Inventory (CBI) (personal; work‐related), gives an estimated effect size of ‐0.49 units on the CBI scale, and a 95% CI of ‐0.97 to 0.00. Given this is less than 1 unit on the CBI scale, which ranges from 0 to 100, this is unlikely to be clinically important.
Academic performance assessed with 2 different questionnaires Follow‐up: 4 weeks to 3.5 months	The academic performance score in the intervention groups was on average 0.6 SDs (1.05 lower to 0.14 lower) lower than in the control groups.		79 (2 RCTs)	Very low^a,d,e,f	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. Due to the very specific nature of the scales used to measure these outcomes, it is difficult to determine how clinically important these differences would be.
Quality of life assessed with 1 questionnaire Follow‐up: 3 to 12 months	The quality of life score in the intervention groups was on average 0.02 SDs (0.28 lower to 0.32 higher) higher than in the control groups.		167 (1 RCT)	Low^d,e,f	As a rule of thumb, an SMD of 0.2 is considered a small effect, 0.5 a moderate effect, and 0.8 a large effect. This study used the Life Satisfaction Questionnaire (LiSat‐9). Given the scores ranged from 9 to 54 on this scale, this is not a clinically important difference.
Deliberate self‐harm	No study reported on this outcome.
Suicidal ideation	No study reported on this outcome.
Suicidal behaviour	No study reported on this outcome.
¹The risk in the intervention group (and its 95% confidence interval) is based on the assumed risk in the comparison group and the relative effect of the intervention (and its 95% CI).  CI: confidence interval; MD: mean difference; OR: odds ratio
GRADE Working Group grades of evidence High certainty: we are very confident that the true effect lies close to that of the estimate of the effect. Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different. Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect. Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.

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^aDowngraded once for serious study limitations due to high risk of bias (deviations from intended interventions).  ^bDowngraded once for serious study limitations due to high risk of bias (lack of information across multiple domains).  ^cDowngraded once due to quality of the evidence for inconsistency. High heterogeneity between studies. ^dNo serious concerns regarding indirectness. All evidence used is directly relevant to the research question. ^eDowngraded once for serious imprecision due to wide confidence intervals. ^fDowngraded one level for high risk of publication bias.

Background

Description of the condition

The emotional status of students entering medical school appears to be similar to the general population, according to depression and anxiety measurements (Leahy 2010; Smith 2007). However, in general, medical students’ mental health tends to begin to suffer during their studies (Dyrbye 2006; Leahy 2010). This suggests that medical education appears to influence the mental well‐being of medical students (Smith 2007).

According to a 2006 systematic review, American and Canadian medical students consistently demonstrate higher levels of psychological distress and a higher prevalence of depression and anxiety than their nonmedical student peers (Dyrbye 2006). An American study reported that 47% of medical students were 'burnt out' and 49% experienced depressive symptoms, with lower scores of mental quality of life (QoL) compared to their peers (Dyrbye 2007). An Australian study found that 48% of medical students were psychologically distressed, more than four times that of their peers (Leahy 2010). A national mental health survey of doctors and medical students in Australia found that these groups are at greater risk of psychological distress compared to the general community, with medical students and doctors who are young or female, or both, being at greatest risk (Beyond Blue 2019; Gunasingam 2015). Compared to their older counterparts, young doctors were found to work longer hours, and suffer from psychological distress and suicidal thoughts to a much greater extent (Beyond Blue 2019).

This review acknowledges that many early‐career professional groups face challenges in high‐stress occupations. In particular, when considering the field of medicine, there are several contributing factors reported by students, which include high expectations, competitiveness, frequent examinations, demanding study load and class content, time pressures, family‐related issues and other extracurricular activities (Pereira 2013). In addition, medical students identified fear of making mistakes or fear of making the incorrect decision about patient care during clinical rotations as stressors (Witt 2019). Burnout is a “state of mental and physical exhaustion” (Ishak 2013), characterised by “emotional exhaustion, depersonalisation and a diminished sense of accomplishment” (Ishak 2009). Burnout is also prevalent among junior doctors, including interns and residents (Gunasingam 2015), as they face many new challenges on entering the medical workforce and learn how to navigate the medical system for the first time. They must learn to manage and communicate with patients as well as other healthcare providers, whilst also handling an increasingly demanding hospital workload.

In spite of this increased burden, and despite greater knowledge of and access to resources and support services, medical students are less likely to utilise such services due to embarrassment and concern over the lack of privacy and confidentiality, and the potential consequences of having a mental illness on their record (Beyond Blue 2019).

Description of the intervention

The concept of mindfulness is broad and difficult to define. Jon Kabat‐Zinn, who is the creator of the Center for Mindfulness in Medicine, Health Care, and Society at the University of Massachusetts Medical School, describes mindfulness as “the awareness that emerges through paying attention on purpose, in the present moment, and non‐judgementally, to the unfolding of experience” (Kabat‐Zinn 2013). Professor Mark Williams of the Oxford Mindfulness Centre argues that “mindfulness also allows us to become more aware of the stream of thoughts and feelings that we experience and to see how we can become entangled in that stream in ways that are not helpful” (Oxford Mindfulness Centre 2012). He argues that “awareness of this kind also helps us notice signs of stress or anxiety earlier and helps us deal with them better” (Oxford Mindfulness Centre 2012).

This systematic review includes any psychological intervention with a primary focus on teaching the fundamentals of mindfulness: self‐regulation of awareness and non‐judgemental acceptance of any phenomena entering one’s attention (Baer 2003). This review was designed to investigate the effects of any mindfulness‐based psychological interventions on the psychological health and well‐being of medical students and junior doctors. It incorporates academic performance as a component contributing to overall well‐being.

This review focuses on mindfulness interventions delivered to undifferentiated groups of medical students and junior doctors. It focuses on interventions applied for preventative purposes, rather than therapeutic mindfulness interventions to treat individuals with diagnosed mental health conditions. However, we have not excluded studies which include some participants who have mental health conditions at baseline. Mindfulness programmes can be conducted through a range of modalities, such as classroom‐based teaching, smartphone applications and meditation retreats.

Lastly, it is noted that there is an emerging discussion in society regarding the adverse effects of mindfulness. There has been evidence of lasting bad effects associated with dysregulated arousal, and transient distress (Britton 2021).

How the intervention might work

Mindfulness has been shown to be beneficial in various populations and contexts, including in people with depression, anxiety disorders, chronic pain and cancer, and with beneficial impacts shown in medical school and prison life (Grossman 2004; Liu 2018; Schell 2019). According to Keng and colleagues, mindfulness “brings about various positive psychological effects, including increased subjective well‐being, reduced psychological symptoms and emotional reactivity, and improved behavioural regulation” (Keng 2011). Medical students and junior doctors may find mindfulness training a useful tool to help improve their ability to cope with stress.

Mindfulness‐based psychological interventions may equip medical students and junior doctors with the ability to choose where they focus their attention, increasing their productivity and their ability to perform under stress (Kabat‐Zinn 2003). Mindfulness may also allow this population to practice more self‐compassion, problem‐solving and a heightened sense of self‐awareness (Allen 2010).

Why it is important to do this review

Mental well‐being and capacity for resilience are key attributes required by medical students and junior doctors, so that they can optimise patient care. Medical school and the junior years as a postgraduate are important periods of time in the career path of a doctor. These periods offer an opportunity to cultivate preventative resilience practices before the accumulation of added responsibility in senior years (Ludwig 2015). Medical students and junior doctors are often time‐poor, with minimal time for leisure or personal pursuits outside of medicine. Therefore, it is important to establish whether mindfulness is an effective intervention which justifies its time commitment.

In this review, we acknowledge that academic performance is highly regarded by medical students and junior doctors. Thus, we have included academic performance as a component of mental well‐being in this population.

Cochrane Reviews have examined the value of mindfulness interventions for women with breast cancer (Schell 2019), the carers of people with dementia (Liu 2018) and people with substance use disorders (Goldberg 2021). A Cochrane review looking at mindfulness interventions for smoking cessation is underway (Jackson 2020). One Cochrane Review has highlighted the role of mindfulness in fostering resilience amongst healthcare students (Kunzler 2020). However, there is yet to be a review that specifically examines the effect of mindfulness‐based interventions on mental health in medical students and junior doctors.

Objectives

To assess the effects of psychological interventions with a primary focus on mindfulness on the mental well‐being and academic performance of medical students and junior doctors.

Methods

Criteria for considering studies for this review

Types of studies

Randomised controlled trials (RCTs), including cluster‐randomised trials, that compared mindfulness‐based psychological interventions to no intervention or waiting‐list control were eligible for inclusion in the review. Randomised cross‐over trials were also eligible, using data only from the first treatment stage to avoid the risk of carry‐over effects.

Types of participants

Eligible participants included any student studying any medical course at any year level, and junior doctors in postgraduate years one, two or three. We excluded studies where all the participants had pre‐existing mental health conditions at baseline and a mindfulness intervention was delivered for treatment. However, we did not exclude studies which included some participants who had mental health conditions as long as the focus was on mindfulness as a preventative intervention delivered to undifferentiated populations. There were no other limitations on participant characteristics, such as age, nationality or baseline health measures.

Types of interventions

Experimental intervention

We included any psychological intervention with a primary focus on teaching the fundamentals of mindfulness as a preventative intervention, including (i) self‐regulation of awareness, and (ii) non‐judgemental acceptance of any phenomena entering one’s attention (Baer 2003).

We included any means of treatment delivery; for example, face‐to‐face, manual‐based, individual or group sessions, web‐based, compact discs, smartphone applications and retreats.

Comparator intervention

No intervention or waiting‐list control.

Types of outcome measures

Changes in mental well‐being through any outcome measure listed below.

Primary outcomes

Anxiety, measured using validated scales such as the Anxiety Inventory (Beck 1988)
Depression, measured using validated scales such as the Depression, Anxiety and Stress Scale (DASS) (Antony 1998)

Secondary outcomes

Stress, measured using validated scales such as the Perceived Stress Scale (Cohen 1983)
Burnout, measured using validated scales such as the Maslach Burnout Inventory (Kristensen 2005)
Academic performance, measured using validated scales such as the Fundamentals of Laparoscopic Surgery Skills Test (Peters 2004)
Quality of life, measured using validated scales such as the Mental Health Continuum ‐ Short Form (Lamers 2011)
Deliberate self‐harm, measured using validated scales such as the Self‐harm Behaviour Questionnaire (Gutierrez 2001)
Suicidal ideation, measured using validated scales such as the Suicidal Ideation Questionnaire (Reynolds 1987)
Suicidal behaviour, measured using validated scales such as the Suicide Behaviours Questionnaire ‐ Revised (Osman 2001)

If a study met the inclusion criteria but did not provide sufficient data necessary to calculate effect estimates, we still included it in the review for narrative analysis, but did not include it in meta‐analysis. For studies where we could not pool data, we described their results in the text of the review, as a narrative synthesis.

Timing of outcome assessment

This review primarily used the first post‐intervention outcome assessment reported by the studies. This was usually immediately post‐intervention but also included time points up to three months after the intervention. We also extracted data on outcomes at up to 6 months, 6 to 12 months, and over 12 months after the intervention.

Hierarchy of outcome measures

We did not give preference to particular outcome measures. Where studies assessed the same outcome, but measured it using different scales, we standardised the results of the studies to a uniform scale before combining them, using standardised mean differences.

Search methods for identification of studies

Electronic searches

We searched the following databases using relevant subject headings (controlled vocabularies) and search syntax, appropriate to each resource.

Cochrane Central Register of Controlled Trials (CENTRAL) Ovid EBM Reviews (August 2021).
MEDLINE Ovid (1946 to 1 October 2021).
Embase Ovid (1947 to 1 October 2021).
PsycINFO Ovid (1806 to 1 October 2021).
CINAHL (Cumulative Index to Nursing and Allied Health Literature) EBSCOhost (1982 to 1 October 2021).
ERIC (Educational Resources Information Center) EBSCOhost (1911 to 1 October 2021).
SCOPUS Elsevier (all available years; 1 October 2021).
US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov; all available years; 1 October 2021).
World Health Organization (WHO) International Clinical Trials Registry Platform (www.who.int/clinical-trials-registry-platform; all available years; 1 October 2021).

We placed no restrictions on date, language or publication status. Search strategies for the Ovid databases are presented in Appendix 1.

Searching other resources

Grey literature

We searched the following sources of grey literature (primarily for dissertations and theses) on 1 October 2021.

Open Grey (www.opengrey.eu).
ProQuest Dissertations & Theses Global (www.proquest.com/products-services/pqdtglobal.html).
DART‐Europe E‐theses Portal (www.dart-europe.eu).
British Libraries e‐theses online service (EThOS) (ethos.bl.uk).
Networked Digital Library of Theses and Dissertations (NDLTD) (search.ndltd.org/).
Open Access Theses and Dissertations (oatd.org).

Reference lists

We checked the reference lists of all included trials and relevant systematic reviews to identify additional trials missed from the original electronic searches (for example, unpublished or in‐press citations).

Correspondence

We contacted trial authors and subject experts for information on unpublished or ongoing trials, or to request additional trial data.

Data collection and analysis

Selection of studies

Two review authors (DT and JH) independently screened titles and abstracts of all the potential studies we identified as a result of the search, and coded them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. If there were any disagreements, a third author (TT) arbitrated. We then retrieved the full‐text study reports or publications, which two review authors (DT and JH) independently screened to identify studies for inclusion. We identified and recorded reasons for exclusion of the ineligible studies. We resolved any disagreement through discussion or, if required, we consulted a third review author (TT). We identified and excluded duplicates and collated multiple reports of the same study, so that each study, rather than each report, is the unit of interest in the review. We recorded the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009), and reported information about the excluded studies in the 'Characteristics of excluded studies' table.

Data extraction and management

We used a data collection form for study characteristics and outcome data, which we piloted on one study in the review. Two review authors independently extracted study characteristics from included studies. We extracted the following study characteristics.

Methods: study design, total duration of study, number of study centres and location, study setting and date of study.
Participants: number randomised, number lost to follow‐up or withdrawn, number analysed, mean age, age range, gender, inclusion and exclusion criteria.
Interventions: intervention, comparison, concomitant medications and excluded medications.
Outcomes: outcomes specified and collected, and time points reported.
Notes: funding for trial, and notable conflicts of interest of trial authors.

Two review authors (JS and PS) independently extracted outcome data from included studies. We resolved disagreements by consensus or by involving a third review author (TT or SG). Two review authors (AJ and PS) transferred data into the Review Manager (RevMan) file (Review Manager 2014). We double‐checked that data were entered correctly by comparing the data presented in the systematic review with the data extraction form.

Main planned comparisons

The main planned comparison was with waiting‐list control or no mindfulness intervention.

Assessment of risk of bias in included studies

Two review authors (JS and TT, SB, SM or MP) independently assessed risk of bias for each study using version two of the Cochrane risk of bias tool (RoB2) (Sterne 2019), outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019b, hereafter referred to as the Cochrane Handbook). (SB, SM and MP have politely declined authorship of this review, and instead have been included in the acknowledgements section.) We resolved any disagreements through discussion or by involving another review author (TT). We assessed the risk of bias of specific results of a trial according to these domains:

bias arising from the randomisation process;
bias due to deviations from intended interventions;
bias due to missing outcome data;
bias in measurement of the outcome; and
bias in selection of the reported result.

We assessed the risk of bias for the outcomes of the included trials that are presented in our summary of findings table. We were interested in quantifying the effect of assignment to the interventions at baseline, regardless of whether the interventions were received as intended (the ‘intention‐to‐treat effect’).

Signalling questions in the RoB2 tool provided the basis for the tool’s domain‐level judgements about the risk of bias. These risk of bias judgement options were 'high', 'some concerns' or 'low'. These algorithm‐generated judgements were then verified by the review authors and revised if necessary. This depended on whether the judgement concerned something likely to affect the ability to draw reliable conclusions from the study. Generally, judging a result to be at a specific level of risk of bias for a specific domain indicates the result has an overall risk of bias at least this severe. However, if ‘some concerns’ arose in multiple domains, we may have decided on an overall judgement of ‘high’ risk of bias for that outcome.

When considering treatment effects, we took into account the risk of bias for the studies that contributed to that outcome.

We assessed the risk of bias for cluster‐randomised trials using the RoB2 tool with the additional domain 'Bias arising from the timing of identification and recruitment of participants'. We gave additional consideration to the recruitment bias that is unique to cluster‐randomised trials. We also used the RoB2 tool for cross‐over RCTs, from which we only used data from the first period. We considered the possibility of selective reporting due to isolated analysis of the first data set rather than the complete study timeline.

We entered and organised our RoB 2 assessments on an Excel spreadsheet (Microsoft Excel RoB2 Macro), and used the Bridges open access repository to share assessments between review authors (Monash University 2020).

Measures of treatment effect

Dichotomous data

We analysed treatment effects for dichotomous outcomes as risk ratios (RR) with 95% confidence intervals (CIs).

Continuous data

For continuous outcomes, we assessed treatment effects using the mean difference (MD) for outcomes measured on the same scale, and the standardised mean difference (SMD) for outcomes measured on different scales. We calculated all treatment effects with 95% CIs. We used a P value of 0.05 or less to indicate statistical significance of effects. We narratively described skewed data reported as medians and interquartile ranges.

Unit of analysis issues

Participants in RCTs are the unit of analysis.

Cluster‐randomised trials

We included and analysed any identified cluster‐randomised trials as long as the trialists undertook proper adjustment for the intra‐cluster correlation, as described in the Cochrane Handbook (Higgins 2019c). In circumstances where trialists did not adjust appropriately, we attempted to correct this.

Cross‐over trials

Due to the risk of carry‐over effects, we only used data from the first phase of cross‐over trials.

Studies with multiple treatment groups

Where studies had additional arms that did not meet the inclusion criteria, we only included data relating to the included intervention and one control arm in the review. If a study had more than two arms that met the inclusion criteria, we split the data in the control arm equally to produce two (or more) pairwise comparisons. If one study presented an outcome as dichotomous data and another study presented the outcome as continuous data, we used an odds ratio (OR) for the dichotomous data and then re‐expressed it as a standardised mean difference (SMD). This allowed us to pool the continuous and dichotomous data sets.

Dealing with missing data

We contacted investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data where possible (e.g. when a study was identified as an abstract only). Where possible, we used the RevMan calculator (Review Manager 2014), a useful calculator tool to assist in data entry of dichotomous, continuous and generic inverse variance outcome types. We used this calculator to calculate missing standard deviations using other data from the trial, such as confidence intervals, based on methods outlined in the Cochrane Handbook (Higgins 2019a). Where this was not possible, and the missing data were thought to introduce serious bias, we explored the impact of including such studies in the overall assessment of results by a sensitivity analysis.

Assessment of heterogeneity

We assessed heterogeneity in two ways. First, we explored the presence of clinical heterogeneity by comparing population groups, interventions and outcomes across trials. In the case of clear clinical heterogeneity, we did not pool the results. We only performed meta‐analysis when trials were sufficiently homogeneous in terms of participants, interventions and outcomes. If there was no obvious clinical heterogeneity, we used statistical tests to determine the presence and level of statistical heterogeneity for each outcome, namely the Chi² test and the I² statistic (Higgins 2003). We interpreted the I² statistic, accompanied by a statistically significant Chi² test, as follows (Deeks 2017):

0% to 40% might not be important;
30% to 60% may represent moderate heterogeneity;
50% to 90% may represent substantial heterogeneity; and
75% to 100% may represent considerable heterogeneity.

This assessment was made with an awareness that the importance of the observed value of I² depended on (i) magnitude and direction of effects, and (ii) strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a confidence interval for I²). If we identified substantial heterogeneity, we reported it and explored possible causes by prespecified subgroup analysis.

Assessment of reporting biases

We performed a formal statistical test for asymmetry (Egger 1997). This review did not undertake a formal assessment of reporting bias using a funnel plot.

Where possible, we attempted to find protocols or trial registrations for included studies to see whether they reported all planned outcomes.

Data synthesis

We undertook meta‐analysis only where this was meaningful; namely, if the treatments, participants and the underlying clinical questions were similar enough for pooling to make sense. The random‐effects model takes into account the fact that different studies are estimating various, yet related, intervention effects (DerSimonian 1986). We used this model, owing to the anticipated variability in the interventions and participants of our included studies. Overall, our primary analysis included all eligible studies.

Furthermore, where meta‐analysis was not possible, we considered whether it was appropriate to use narrative synthesis methods, as described in Chapter 12 of the Cochrane Handbook (Schünemann 2019). However, implementation of these methods was not required in this review.

Subgroup analysis and investigation of heterogeneity

We planned to carry out the following subgroup analyses for any outcomes with substantial heterogeneity. We used the formal test for subgroup differences in Review Manager (Review Manager 2014), and based our interpretation on this. We planned to undertake subgroup analyses to investigate the impact of the following factors on the magnitude of the treatment effect.

Intervention duration: less than 3 months, 3 to 6 months, and 6 to 12 months.
Proportion of study population meeting study‐defined levels of compliance with home meditation: 0 to 50%, over 50%.

Given the complexity of ways the intervention may be delivered, we also intended to explore the impact of intervention intensity and report these findings narratively.

Sensitivity analysis

We used sensitivity analyses to assess the robustness of results to key assumptions, such as the impact of imputed data and studies at high risk of bias.

Summary of findings and assessment of the certainty of the evidence

We created a summary of findings table using these outcomes:

anxiety;
depression;
stress;
burnout;
academic performance;
quality of life;
deliberate self‐harm;
suicidal ideation;
suicidal behaviour.

We used the five GRADE considerations (overall risk of bias, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of a body of evidence as it relates to the studies which contributed data to the meta‐analyses for the prespecified outcomes. We incorporated the overall RoB2 judgement into our GRADE assessment. We used methods and recommendations described in Chapter 14 of the Cochrane Handbook (Schünemann 2019), and generated the table using GRADEpro software (GRADEpro GDT). We justified all decisions to downgrade the certainty of studies using footnotes, and we made comments to aid readers' understanding of the review where necessary.

Two review authors made judgements about evidence certainty independently, resolving disagreements through discussion or by involving a third review author (TT or SG). We justified and documented our judgements, and incorporated them into our reporting of each outcome's results.

Results

Description of studies

See 'Characteristics of included studies' tables.

Results of the search

In total, our searches identified 877 records. Of these, we imported 875 records for screening. We removed 236 duplicates, and screened the titles and abstracts of the remaining 639 records. We excluded 557 irrelevant reports. We obtained the remaining 73 reports for full‐text screening. After reading the full texts, we excluded 51, as they did not fulfil our review eligibility criteria. We have reported the reasons for exclusion in the 'Characteristics of excluded studies' table. We identified eight ongoing studies. We identified four studies potentially meeting our inclusion criteria, for which additional information is being sought from authors. These studies are awaiting classification. We included 10 studies in our systematic review (Figure 1).

Included studies

Ten studies met the criteria for inclusion in the review, and were included in meta‐analyses.

Design

All included studies were RCTs. One study used a cluster‐randomised design (Van Djik 2017), where clerkship groups were randomised, rather than individual participants. No included studies used a cross‐over design. All 10 studies included two arms and compared mindfulness versus no mindfulness, waiting list or usual care (Cheung 2020; Damião Neto 2020; Danilewitz 2016; Erogul 2014; Ireland 2017; Lebares 2018; Paholpak 2012; Phang 2015; Van Djik 2017; Yang 2018).

Sample size

This current review includes 10 studies with a total of 731 participants. Study sample sizes ranged from 21 participants (Lebares 2018), to 167 participants (Van Djik 2017).

Time period

All studies were published between 2010 and 2020.

Setting

Four studies were conducted in the USA (Cheung 2020; Erogul 2014; Lebares 2018; Yang 2018), one in Canada (Danilewitz 2016), one in Brazil (Damião Neto 2020), one in Australia (Ireland 2017), one in the Netherlands (Van Djik 2017), and two in Asia (Paholpak 2012; Phang 2015). Three studies recruited participants through workplace settings (Cheung 2020; Ireland 2017; Lebares 2018), and the remaining seven studies recruited participants through academic university settings (Damião Neto 2020; Danilewitz 2016; Erogul 2014; Paholpak 2012; Phang 2015; Van Djik 2017; Yang 2018).

Participants

Three studies recruited junior doctors in postgraduate years one, two or three (Cheung 2020; Ireland 2017; Lebares 2018), and the remaining seven studies included students studying any medical course at any year level (Damião Neto 2020; Danilewitz 2016; Erogul 2014; Paholpak 2012; Phang 2015; Van Djik 2017; Yang 2018). There were no limitations on participant characteristics, such as age, nationality or baseline health measures. All included studies provided mindfulness as a preventative intervention rather than a therapeutic treatment.

Intervention

In terms of duration, the shortest intervention period was less than seven days (Cheung 2020). Two studies had an intervention duration of approximately one month: for Paholpak 2012, it was four weeks, and for Yang 2018, it was 30 days. Phang 2015 had an intervention duration of five weeks. Four studies had an intervention duration of 8 weeks (Danilewitz 2016; Erogul 2014; Lebares 2018; Van Djik 2017), and one study had an intervention duration of 10 weeks (Ireland 2017).

Seven studies utilised a didactic weekly teaching session on mindfulness which ranged from one to two hours weekly (Damião Neto 2020; Danilewitz 2016; Erogul 2014; Ireland 2017; Lebares 2018; Phang 2015; Van Djik 2017). Two studies used an audio‐guided session daily for 20 minutes (Paholpak 2012; Yang 2018), and one study used a mindfulness video before an academic activity (Cheung 2020). Five studies also used self‐directed home meditation practice in conjunction with didactic teaching sessions (Damião Neto 2020; Erogul 2014; Lebares 2018; Phang 2015; Van Djik 2017). Three studies used a waiting‐list control (Danilewitz 2016; Phang 2015; Yang 2018). Other control interventions included treatment as usual or no intervention (Erogul 2014; Ireland 2017; Lebares 2018; Paholpak 2012; Van Djik 2017). Three controls in studies distributed information about the importance of physical activity (Cheung 2020; Damião Neto 2020; Lebares 2018).

In terms of delivery, nine of the ten studies used either trained instructors or relevant health professionals to deliver mindfulness in various mediums (Cheung 2020; Damião Neto 2020; Danilewitz 2016; Erogul 2014; Lebares 2018; Paholpak 2012; Phang 2015; Van Djik 2017; Yang 2018). Ireland 2017 did not provide information on who delivered their mindfulness intervention. In terms of how the mindfulness intervention was delivered, three studies delivered mindfulness to participants individually (Cheung 2020; Danilewitz 2016; Yang 2018), whilst two studies delivered mindfulness through group teaching (Paholpak 2012; Van Djik 2017). Five studies used a combination of didactic teaching or group mindfulness sessions as well as at‐home personal meditation (Damião Neto 2020; Erogul 2014; Ireland 2017; Lebares 2018; Phang 2015).

Outcomes

We describe the outcomes for each study in detail in the 'Characteristics of included studies' tables.

The primary outcomes were depression and anxiety symptom levels, measured by differing scales at the end of mindfulness interventions (28 days to 10 weeks). Depression was measured at baseline and post‐intervention, which varied from 4 weeks to 14 weeks. The studies used several scales to measure symptom levels:

Depression, Anxiety and Stress Scale (DASS‐42) – 42‐item self report questionnaire (Lovibond 1995);
Depression, Anxiety and Stress Scale (DASS‐21) – 21‐item short‐form version of DASS‐42 (Lovibond 1995);
the Symptom Checklist 90 (SCL‐90) – 90‐item questionnaire (Derogatis 1994).

Anxiety was measured at baseline and post‐intervention, and studies used the scales listed above.

The secondary outcomes were academic performance, burnout, stress and quality of life. Academic performance was measured post‐intervention, and used psychiatry examination scores, and measures of skill in surgical and procedural interventions. Burnout was measured using the Copenhagen Burnout Inventory (Kristensen 2005). Stress outcomes were measured using the Perceived Stress Scale, DASS‐42 and DASS‐21. Quality of life symptoms were measured using the Life Satisfaction Questionnaire (Li‐Sat 9).

None of the included studies reported on these outcomes:

self‐harm;
suicidal ideation; and
suicidal behaviour

Excluded studies

After de‐duplication and discarding irrelevant reports, we obtained the full texts of 73 reports. After reading the full texts, we excluded 51 studies. The reasons for exclusion are detailed in the 'Characteristics of excluded studies' tables, and are outlined below.

Mindfulness not used as the intervention (24) (Akhani 2019; Alexander 2015; Axisa 2019; Chinai 2016; Dandekar 2013; Holtzworth‐Munroe 1985; IRCT20191107045358N; Knol 2020; Koh 2008; Kon 2019; Kondam 2017; Kraemer 2015; Mache 2018; Mascara 2016; Moir 2016; Nathan 1987; Oman 2006; Ospina‐Kammerer 2003; Rosenzweig 2003; Ritzenthaler 2018; Saoji 2016; Saravanan 2014; Taylor 2020; Wetzel 2011; Whitehouse 1996).
Not a randomised controlled study design (13) (Babbar 2019; Chanu 2014; Chen 2016; Fendel 2020; Herres 2019; Hutton 2019; Krane 2019; Krasner 2009; Oró 2020; Pateropoulos 2018; Rodriguez 2014; Rosenzweig 2003; Zazulak 2017).
Participant population did not involve medical students or junior doctors (12) (Amutio 2015; Christopher 2016; Dunne 2019; Grepmair 2007; Jain 2007; Lambert 2019; Moody 2012; Ritvo 2020; Shapiro 1998; Siedsma 2015; Simons 2015; Swift 2017).
Ineligible outcomes (2) (Fernando 2017 – wrong outcome: looking at compassion in medicine; Lebares 2021).

Ongoing studies

We identified eight ongoing studies (ACTRN12617000290392; NCT03148626; NCT03514862; NCT03895190; NCT03330665; NCT04026594; Perula‐de Torres 2019; Warnecke 2011).

Studies awaiting classification

For four studies, the information available was insufficient to determine eligibility. We have asked the authors for further information and are awaiting their response (De Vibe 2013; Fendel 2021; Kuhlmann 2015; NCT03687450).

Risk of bias in included studies

This review used version two of the Cochrane risk of bias tool (RoB2) (Sterne 2019), outlined in the Cochrane Handbook (Higgins 2019b). Risk of bias assessments for each outcome, including all domain judgements and support for judgements, is located in the risk of bias section (after the 'Characteristics of included studies'), beside each of the forest plots. Given the small number of included studies, we did not undertake a formal assessment of reporting bias using a funnel plot.

The RoB 2 judgements for all study results per outcomes and for all domains are available in a risk of bias table, including consensus responses to the signalling questions (10.26180/15079344), and are also briefly summarised below.

Overall risk of bias by study

Across most outcomes, the overall risk of bias was 'some concerns'. There were two exceptions that we judged to have an overall high risk of bias. One study did not provide information regarding concealment, participant compliance or dropout, or amount of outcome data available (Paholpak 2012). No pre‐specified analysis plan was available, so it remains unclear if selective reporting occurred (Paholpak 2012). The second study at high risk of bias did not provide information regarding allocation sequence or concealment, or information compliance, which made it difficult to assess deviation from the intended intervention (Ireland 2017). There was insufficient information about how much outcome data were available (Ireland 2017). No prespecified analysis plan was available, so it remains unclear if selective reporting occurred (Ireland 2017).

Given the small number of included studies looking at each of the primary and secondary outcomes, we did not undertake sensitivity or subgroup analyses.

Overall risk of bias by outcome

The following section summarises the risk of bias per outcome for all outcomes which are included in the summary of findings table (Table 1).

Anxiety

We judged three studies as having 'some concerns' for risk of bias (Cheung 2020; Damião Neto 2020; Danilewitz 2016), and a fourth study as being at high risk of bias due to deviations from intended interventions (Paholpak 2012).

Depression

Four studies reported depression outcomes immediately post‐intervention (Damião Neto 2020; Danilewitz 2016; Lebares 2018; Paholpak 2012). We assessed three studies as having 'some concerns' for risk of bias (Damião Neto 2020, Danilewitz 2016, Lebares 2018), and the fourth study as high risk of bias due to deviations from intended interventions (Paholpak 2012).

Stress, immediately post‐intervention

Eight studies reported stress outcomes immediately post‐intervention (Cheung 2020; Damião Neto 2020; Danilewitz 2016; Erogul 2014; Ireland 2017; Lebares 2018; Phang 2015; Yang 2018). We judged seven of these as having 'some concerns' for risk of bias, and the remaining study, Ireland 2017, as high risk of bias due to lack of information across multiple domains.

Stress, end of long‐term follow‐up

Four studies reported stress outcomes at longer‐term time points (Erogul 2014; Ireland 2017; Phang 2015; Yang 2018). We judged all four studies as having 'some concerns' for risk of bias.

Burnout

Three studies reported burnout outcomes immediately post‐intervention (Cheung 2020; Ireland 2017; Lebares 2018). We assessed all three studies as having 'some concerns' for risk of bias.

Academic performance

Two studies reported academic performance immediately post‐intervention (Lebares 2018, Paholpak 2012). There were 'some concerns' for risk of bias for Lebares 2018. We assessed Paholpak 2012 as having high risk of bias due to deviations from intended interventions.

Quality of life

One trial reported changes in the Life Satisfaction Questionnaire (LiSat‐9), a quality of life measure (Van Djik 2017). We judged this study as having 'some concerns' for risk of bias.

Effects of interventions

See: Table 1