Adverse effects of electroconvulsive therapy

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the adverse effects of electroconvulsive therapy across indications in children, adolescents, adults and older people.

Background

Description of the condition

Electroconvulsive therapy (ECT) is usedfor a range of psychiatric conditions, including depression, mania and bipolar disorder, schizophrenia, catatonia, and obsessive‐compulsive disorder (OCD) (Kellner 2020).

Depression

The clinical diagnosis of depression is defined in the main classificatory diagnostic systems, the International Classification of Diseases (ICD) (WHO 1992) and Diagnostic and Statistical Manual of Mental Disorders (DSM) (APA 2013)), by symptoms forming a syndrome and causing impairment (Malhi 2018). Depending on the diagnostic system, a depressive episode is characterised by a period of almost daily depressed mood, reduced energy or fatigue, or loss of interest or pleasure in activities, accompanied by other symptoms such as difficulty concentrating, feelings of worthlessness, excessive or inappropriate guilt, hopelessness, recurrent thoughts of death or suicide, changes in appetite or sleep, and psychomotor agitation or retardation (APA 2013; WHO 1992).

The lifetime prevalence of depression varies geographically. Among 10 high‐income countries, which included Germany, Japan, and the US, lifetime prevalence was estimated at a mean of 14.6% (Bromet 2011). Among eight low‐ to middle‐income countries, which included Colombia, Mexico and Ukraine, it was estimated at a mean of 11.1% (Bromet 2011). The World Health Organization (WHO) estimates that more than 264 million people suffer from depression worldwide (WHO 2019); such estimates should be interpreted with caution, however, as they are based on diagnostic categories thatlikely have low validity in many parts of the world (Summerfield 2008).

Most people with moderate to severe depression do not achieve remission following initial treatment with antidepressants, which is the usual recommended first‐line treatment, ideally in combination with psychotherapy (RANZCP 2018; WFSBP 2017). The largest trial to investigate the effectiveness of antidepressant treatment for depression, designed to mimic clinical practice, found that approximately one‐quarter of the participants achieved remission after initial treatment with a selective serotonin reuptake inhibitor (SSRI) (Kirsch 2018); remission was defined in the trial as a total score on the Hamilton Depression Rating Scale (Hamilton 1967) of 7 or lower (Kirsch 2018). This  rate of remission, however, likely overestimates the benefit because, using these common criteria, as many as half of the patients classified as being in remission do not consider themselves to be in remission (Zimmerman 2006); other factors such as spontaneous improvement and placebo effects may partially or fully explain the observed improvement in individual patients. One‐quarter of patients with depression may go on to develop chronic depression(Boschloo 2014). In situations where patients are not helped by available pharmacological or psychological treatments or develop a more severe course of depression, ECT can be considered a treatment option (CANMAT 2016; NICE 2009; WFSBP 2013).

Mania and bipolar disorder

The definition of the clinical diagnosis of bipolar disorder differs between the ICD (WHO 1992) and the DSM (APA 2013)). The tenth revision of the ICD (ICD‐10) (WHO 1992) defines bipolar disorder as a condition characterised by the occurrence of two or more episodes of depression and hypomania or mania that are sufficiently severe to cause a change in functioning; patients with two or more episodes of hypomania or mania, but not depression, are also classified as having bipolar disorder, while patients with recurring depression but no hypomanic or manic episodes are not. The fifth edition of the DSM (DSM‐5) (APA 2013) distinguishes between two types of bipolar disorder: bipolar I disorder, defined by the occurrence of at least one manic episode, but not necessarily any depressive episodes, and bipolar II disorder, defined by the occurrence of at least one hypomanic episode and at least one major depressive episode in the absence of prior manic episodes.

Depending on the diagnostic system, a manic or hypomanic episode is characterised by a period of symptoms of abnormally and persistently elevated, expansive or irritable mood and abnormally and persistently increased goal‐directed activity or energy, accompanied by other symptoms such as inflated self esteem, decreased need for sleep, pressure to keep talking, flight of ideas or racing thoughts and distractibility; with such symptoms occurring daily, for most of the day (APA 2013; WHO 1992). Manic episodes, in contrast to hypomanic episodes, are characterised by disturbances that are sufficiently severe to cause marked impairment in functioning (APA 2013; WHO 1992). According to ICD‐10, a diagnosis of a manic or hypomanic single episode is given to patients fulfilling criteria for a manic or hypomanic episode, respectively, but who do not fulfil criteria for bipolar disorder. ICD‐10 additionally specifies a diagnosis of a mixed state characterised by concurring or rapidly shifting manic and depressive symptoms in patients who have previously had at least one other affective episode (hypomania, mania, depression or mixed state) (WHO 1992); in DSM‐5, the presence of mixed symptoms is instead acknowledged by assigning a mixed feature specifier to a diagnosis of hypomania, mania or depression (APA 2013). The diagnostic criteria for mixed states thus differ between diagnostic systems, have undergone changes in both diagnostic systems over time, and are surrounded by some controversy (Malhi 2017; Parker 2019).

The lifetime prevalence of bipolar disorder varies geographically. Among eleven middle‐ to high‐income countries, prevalence is estimated at a mean of 0.6% for bipolar I disorder and 0.4% for bipolar II disorder (Merikangas 2011). Bipolar I prevalences range from just above 0% in countries such as Bulgaria and India to 1% in countries such as Mexico and the US (Merikangas 2011). The prevalence of bipolar I disorder in prepubertal children and adolescents has been estimated at a mean of 0.6% across nine middle to high‐income countries, with prevalences ranging from 0% in countries such as Brazil, Ireland and Turkey, to 2% in Mexico and Canada (Van Meter 2019). However, the diagnosis of bipolar disorder and its prevalence in prepubertal children and adolescents has been controversial (Malhi 2020; Parry 2019; Van Meter 2019). The WHO estimates that 45 million people suffer from bipolar disorder worldwide (WHO 2019). However, as these estimates are based on diagnostic systems with likely low validity in many parts of the world, they should be interpreted with caution (Summerfield 2008).

Many patients with bipolar depression do not recover with initial or secondary pharmacological treatment (Parikh 2010). In situations where the patients' condition is not sufficiently alleviated by available pharmacological or psychological treatments or where patients develop a more severe acute affective episode, ECT is considered a treatment option (APA 2003; BAP 2016; CANMAT 2018).

Schizophrenia

Depending on the diagnostic system, the clinical diagnosis of schizophrenia is defined by the presence of a number of symptoms that may include delusions, hallucinations, disorganised speech, catatonic behavior (e.g. inhibited movement, agitation or fixture of posture), negative symptoms (e.g. loss of motivation in life and activities), and a reduced level of functioning (APA 2013; WHO 1992).

The lifetime prevalence of schizophrenia varies geographilly. A well‐conducted population‐based survey in Finland found a lifetime prevalence of 0.87% (Perala 2007). Across populations from 46 countries such as Argentina, Botswana, Greece and the United States, the lifetime prevalence has been estimated at a median of 0.4% (Saha 2005). The majority of patients diagnosed with schizophrenia experience relapse after treatment of an acute episode, and 10% to 45% of patients are characterised as treatment resistant (Carbon 2014). The WHO estimates that schizophrenia affects 20 million people worldwide (WHO 2019); such estimates should be interpreted with caution, however, as they are based on diagnostic categories thatlikely have low validity in many parts of the world (Summerfield 2008).

Moderate‐quality evidence indicates that ECT may have some benefit in treatment‐resistant schizophrenia (Sinclair 2019). Guidelines consider ECT a treatment option both for acute episodes of schizophrenia and treatment‐resistant schizophrenia (APA 2020; RANZCP 2016; RANZCP 2019).

Catatonia

Catatonia is a condition that can occur in both schizophrenia and mood disorders (Grover 2019) and is characterised by psychomotor disturbances, such as stupor, catalepsy (e.g. rigidity and fixture of posture), mutism (i.e. inability to speak), mannerism (e.g. carrying out odd, exaggerated actions), rigidity and agitation (APA 2013; WHO 1992).

ECT is among the recommended treatments for catatonia in clinical guidelines (Pelzer 2018; RANZCP 2019).

Obsessive compulsive disorder

Although ECT is used for the treatment for OCD and is recommended by experts (Kellner 2020), major guidelines do not recommend it for the treatment of OCD (Koran 2007; NICE 2005; RANZCP 2019).

Other disorders

ECT may also be used to treat non‐psychiatric conditions such as Parkinson's disease, status epilepticus and delirium (Kellner 2020); some experts also consider ECT effective for preventing suicide across psychiatric disorders (Fink 2014; Prudic 1999).

Description of the intervention

ECT involves the application of electricity to the scalp in order to induce a generalised tonic‐clonic seizure. ECT for the treatment of depression is usually delivered two to three times per week (Kellner 2012) in a series of six to 12 treatments in total (Lisanby 2007). ECT for acute delirious mania may be delivered daily (Baghai 2008). It is considered best practice to administer ECT under anaesthesia together with muscle relaxant medication, in what is termed 'modified' ECT (CPA 2010; RANZCP 2019; RCPSYCH 2019). These methods were introduced to reduce treatment complications such as pain, panic and fractures (APA 1978). However, 'unmodified' ECT, administered without anaesthesia, is still being practised around the world, including in parts of Asia, Africa, South America and Europe (Leiknes 2012). Different regimens of intravenous sedatives or hypnotics may be used; the evidence is uncertain as to whether different types of anaesthetic agents have an effect on the efficacy of ECT for depression (Lihua 2014) or mania (Kadiyala 2017). ECT for catatonia and severe bipolar depression in patients aged 13 years and older, who are considered treatment‐resistant or who require a rapid response due to the severity of the condition or a medical condition, was reclassified by the US Food and Drug Administration (FDA) in 2018 from a class III ('high risk') device to a class II ('moderate risk') device (FDA 2018); ECT for the treatment of mania is classified as a class III device.

ECT is traditionally administered with a 'brief' pulse width, defined as pulses of 0.5 to 2.0 milliseconds in duration (CPA 2010; RANZCP 2019; RCPSYCH 2019). Brief‐pulse wave ECT has been associated with fewer cognitive adverse effects, compared with sine wave ECT (Sackeim 2007) and is the recommended stimulus method in current guidelines (APA 2001; CPA 2010; RANZCP 2019; RCPSYCH 2019). The sine‐wave stimulus employed by the earliest ECT devices delivered an electrical charge in excess ofthe amount needed to efficiently elicit a seizure, leading to more frequent or severe cognitive adverse effects compared with brief‐pulse ECT (CPA 2010); sine wave ECT is, however, still practised around the world (Leiknes 2012). Ultrabrief‐pulse wave ECT (0.25 to 0.3 milliseconds) has been available for the last decade, and may be associated with fewer cognitive adverse effects, compared with brief‐pulse wave ECT (Loo 2008; Sackeim 2008). However, it has been suggested to have a smaller effect, depending on the electrode placement (Brus 2017; Tor 2015).

Common electrode placements include bitemporal, right unilateral and bifrontal (Lisanby 2007). Generally, bitemporal ECT is considered to involve the highest risk of retrograde amnesia and is inone guideline (RANZCP 2019) recommended not to be used as the initial form of ECT treatment given, unless there are specific reasons to do so. Other guidance, however, states that bitemporal ECT is preferred for acute mania (CPA 2010).

In clinical practice, the choice of stimulus current dose depends on both electrode placement and pulse‐width (CPA 2010; RANZCP 2019). Generally, higher doses relative to the seizure threshold may be needed when reducing the pulse width, to achieve a similar effect Loo 2008). Depending on the pulse‐width, the recommended dose level is approximately 1.5 times the seizure threshold for bitemporal and bifrontal ECT and approximately six times the seizure threshold for right unilateral ECT (CPA 2010; RANZCP 2019).

The choice of treatment approach is recommended to be informed by balancing the need for speed of response, the urgency of the clinical situation, the patient’s previous response and concern regarding potential cognitive side‐effects (RANZCP 2019). All electrode placements and stimulus forms, however, appear to be associated with cognitive adverse effects, including a risk of retrograde amnesia (Sackeim 2008; Sackeim 2014).

Multiple guidelines recommend consideration of ECT for the treatment of different psychiatric conditions. Guidelines recommend ECT for the treatment of acute depressive episodes with certain clinical features, such as psychosis (APA 2010; CANMAT 2016; McIntyre 2017; RANZCP 2015; WFSBP 2013); catatonia (APA 2010; RANZCP 2015; CANMAT 2016); where the patient refuses to eat or drink (APA 2010; RANZCP 2015; WFSBP 2013); or where there is a high risk of suicide (APA 2010; CANMAT 2016; RANZCP 2015; WFSBP 2013). Guidelines recommend ECT for treatment‐resistant acute depressive episodes (CANMAT 2016; NICE 2009; WFSBP 2013); in patients who have had previous response to ECT (APA 2001; CANMAT 2016; RANZCP 2015; WFSBP 2013); as a first‐line treatment for depression in pregnant women where medication is considered contraindicated, especially during the first trimester (WFSBP 2013); in severe depression with certain clinical features, and in treatment‐resistant depression (CANMAT 2016). Two guidelines suggest ECT as the treatment of choice for severe depression during pregnancy, without specifying any particular clinical features or situations (APA 2010; RANZCP 2015). Independent of its effect on depression, ECT is also considered effective for suicidal ideation (Kellner 2005).

Guidelines recommend ECT for the treatment of bipolar depression (APA 2003; BAP 2016; CANMAT 2018; CINP 2017; RANZCP 2015; WFSBP 2010), acute manic episodes (APA 2003; BAP 2016; CANMAT 2018; CINP 2017; NICE 2014; RANZCP 2015; WFSBP 2009), and for the treatment of treatment refractory mixed episodes (APA 2003; RANZCP 2015; WFSBP 2018). Several guidelines specifically recommend that ECT should be considered for the treatment of acute affective episodes in women with bipolar disorder during pregnancy (APA 2003; BAP 2016; CINP 2017; RANZCP 2015; WFSBP 2009).

Guidelines recommend consideration of ECT for the treatment of patients with schizophrenia who are considered treatment‐resistant (WFSBP 2012; RANZCP 2016; APA 2020), or catatonic (WFSBP 2012; APA 2020), or in those in those who have a significant suicide risk (APA 2020).

In children and adolescents specifically, guidelines recommend that ECT should be considered for both affective disorders and for schizophrenia. Thus, guidelines recommend that ECT is available for the treatment of severe affective or psychotic illness and catatonia when pharmacological treatment is considered ineffective (Birmaher 2007; Ghaziuddin 2004; Grover 2019; RANZCP 2015) and that ECT should specifically be available to pre‐adolescent children when "clinically appropriate" (RANZCP 2019). One guideline states that non‐controlled reports suggest that ECT is useful for depressed psychotic adolescents (McClellan 2007). ECT is also recommended to be considered for the treatment of bipolar depressive episodes (Gautam 2019; McClellan 2007) and manic episodes (McClellan 2007) not responding to medication therapies and for adolescents with schizophrenia who are considered severely impaired when medications are not helpful or cannot be tolerated (McClellan 2013).

Some aspects of the current practice of ECT, while varying across regions, are not in alignment with international guidelines. Thus, despite recommendations to use unilateral ECT by several international guidelines, evidence shows it is still common practice to use bilateral ECT (Bjornshauge 2019; Leiknes 2012).

There are important known adverse effects of ECT (Andrade 2016), including nausea, headache and myalgia, prolonged seizures, status epilepticus, and cardiac events such as asystole and myocardial infarction (Andrade 2016; CPA 2010). Unmodified ECT may, in addition to those adverse effects, be associated with a risk of loosened or broken teeth, joint dislocation, bone fracture, spinal fracture, and muscle or ligament injuries (Andrade 2012). Cognitive impairment is recognised as a criticaladverse effect of ECT (APA 1978). Cognitive effects commonly include postictal confusion states and anterograde amnesia; ECT is also associated with retrograde amnesia, including impairment of autobiographical memory (APA 2001; CPA 2010; RANZCP 2019), which can be persistent (APA 2001; Sackeim 2007). Amnesia for autobiographical information is considered the most critical adverse cognitive effect of ECT (Sackeim 2014), its intensity seemingly dependent on the electrode placement and the pulse width (Fraser 2008). The clinical methods used to assess retrograde amnesia, however, have been a subject of discussion (Sackeim 2014; Semkovska 2014) and there may be discrepancies between the objective assessments of cognitive deficits in general and the subjective reporting of them (Svendsen 2012) .

An estimated total of 1.5 million people are being treated with ECT annually worldwide for any indication (Leiknes 2012), the use varying by country and region. Affective disorders are the most common indication for ECT across the US, Western Europe, New Zealand and Australia while schizophrenia and related disorders are more common indications for ECT across South America, Africa and some Eastern European countries (Leiknes 2012). ECT is used less often in children and adolescents compared with adults (Ghaziuddin 2004), but data regarding the use in children and adolescents is scarce.

In some countries, special legal restrictions are imposed on the administration of ECT (Leiknes 2012). The administration of ECT under involuntary conditions occurs worldwide but the extent varies between countries (Leiknes 2012). The United Nations has called for member states to ban all forced and non‐consensual use of ECT (UN 2013; UN 2018) and to reframe and recognise such ECT practices as constituting torture or other cruel, inhuman or degrading treatment (UN 2018). In India, the use of unmodified ECT has been prohibited by law (Duffy 2019; Government of India 2017). Several US states have prohibited the use of ECT in children and adolescents (Livingston 2018) and in Australia, the state of Western Australia has prohibited the use of ECT in children under age 14 years (GWA 2018). WHO has stated that there is no indication for ECT in minors and that it should therefore be prohibited by legislation (WHO 2005). Some psychiatrists and ECT experts advocate for the continued use of ECT in both prepubertal children and adolescents for certain clinical indications and for the removal of impediments to ECT access in that population (Wachtel 2011).

How the intervention might work

Although there are many theories (Michael 2009), the mechanism of action of ECT is unknown. Among current hypotheses, the more prominent relate to effects of the generalised seizure, actions on the neuroendocrine system through engagement of central brain stem structures and neurotrophic effects induced by seizure activity in the limbic system (Bolwig 2014).

Why it is important to do this review

Among existing systematic reviews of ECT for depression (Chen 2017; Kho 2003; Mutz 2019; Papadimitropoulou 2017; Ren 2014; UK ECT Review Group 2003; Van der Wurff 2003), some compared ECT treatment only with repetitive transcranial magnetic stimulation (rTMS) (Chen 2017; Ren 2014), other brain stimulation techniques or sham treatment (Mutz 2019), and not with other treatment modalities. Other reviews considered only elderly patients (Van der Wurff 2003) or patients with only treatment‐resistant depression (Papadimitropoulou 2017). Repetitive transcranial magnetic stimulation is also a recommended treatment option for individuals with depression whose condition is not sufficiently helped by initial treatment (CANMAT 2016; RANZCP 2018). It involves the induction of electrical currents using focused magnetic field pulses via a coil placed against the scalp, which can be administered without the need for anesthesia (Hallett 2007). Apart from a systematic review of the evidence of ECT compared with rTMS (Ren 2014), no systematic review for the acute treatment of depression assessed the certainty of the evidence. Beyond a Cochrane Review of modified ECT for depression in the elderly (Van der Wurff 2003), which assessed several prespecified adverse effects; and a systematic review of ECT that assessed mortality (UK ECT Review Group 2003), none of the existing reviews investigated specific adverse effects of ECT. No systematic review has specifically assessed the beneficial and adverse effects of ECT for depression in children and adolescents; two systematic reviews did not state any age eligibility criteria but did not mention children or adolescents (Ren 2014; UK ECT Review Group 2003).

Existing systematic reviews of ECT for bipolar disorder considered only acute depressive episodes in adults, not manic or mixed episodes, and compared ECT with only sham ECT or rTMS (Chen 2017; Mutz 2018; Mutz 2019; Ren 2014), and not other treatment modalities or no treatment. Of those reviews, only one used GRADE to assess the certainty of the evidence, finding it to be moderate (Ren 2014). None of the reviews systematically investigated specific adverse effects beyond cognition. There is no Cochrane Review of ECT for acute affective episodes in patients with bipolar disorder. Three of the reviews (Chen 2017; Mutz 2018; Mutz 2019) specifically stated to investigate adults only and one did not specify age criteria but also included studies of adults only (Ren 2014).

Of existing systematic reviews of ECT for schizophrenia that both assessed specific adverse effects of ECT and evaluated the certainty of the evidence (Wang 2015; Sinclair 2019), both included only studies of patients with treatment‐refractory schizophrenia, one investigated adults only (Sinclair 2019) and one investigated only ECT treatment as an adjunctive to antipsychotic medication (Wang 2015).

Systematic reviews focusing exclusively on the adverse effects on autobiographical memory or broadly on retrograde amnesia of ECT were either considering comparisons between different stimulation methods (Verwijk 2012) only, rather than comparisons between ECT and other treatment modalities; or investigated only within‐subject changes in non‐controlled designs (Semkovska 2010) that are inherently unable to inform on the effect of ECT treatment. No systematic review assessed the risk of bias in the included studies or assessed the certainty of the evidence. No systematic review of the adverse effects of ECT considered the breadth of the evidence across conditions.

Given the limitations of existing systematic reviews, a comprehensive synthesis of the evidence of adverse effects of ECT in children and adults is needed. As randomised trials of ECT may not be large enough to detect important but rare adverse effects (individual studies may not have captured important adverse effects), and as the mechanism of harm and the susceptibility to adverse effects would be expected to be reasonably similar across the conditions for which ECT is usually prescribed, it may be beneficial to include studies across conditions when assessing adverse effects of ECT. We therefore wish to conduct a systematic review of the adverse effects of ECT across conditions. The review will supplement our planned reviews of beneficial and adverse effects of ECT for the treatment of depression and acute affective episodes in bipolar disorder, respectively. 

Objectives

To assess the adverse effects of electroconvulsive therapy across indications in children, adolescents, adults and older people.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised trials, including cross‐over trials and cluster‐randomised trials. For cross‐over trials, only the results from the first randomised period will be included, as affective symptoms may be fluctuating, the condition may be episodic and carry‐over effects of ECT are likely.

As we suspect that available randomised trials address the review question only indirectly or incompletely, e.g. because the outcomes of interest were not collected or were rare, we will also include non‐randomised studies. For non‐randomised studies, we will include studies with the following design characteristics, based on balancing availability of studies (determined through scoping availbale non‐randomised studies) with inclusion of studies that have the potential to estimate causality with the least possible risk of bias (Reeves 2019). We will not include studies based on their study design labels as e.g. cohort studies or cross‐sectional studies, as such labels are often used in inconsistent ways (Reeves 2019). We will thus include studies in which a) ECT and comparator were delivered to individuals or clusters of individuals, b) outcome data were available once before and after, or after only, delivery of ECT and comparator, c) the intervention effect was estimated by the difference between groups, d) groups were formed by helthcare decision makers or participant's preferences. We will include non‐randomised studies regardless of the method used to control for confounding and whether potential confounders and outcome variables were measured before intervention. 

Types of participants

Participant characteristics

We will include participants of both sexes, and of all ages.

Diagnosis

We will include participants with any acute psychiatric or non‐psychiatric condition. We will not consider studies that include participants who are considered to be in remission of their respective conditions (e.g. maintenance studies allocating patients to ECT after achieving remission during a period of treatment for an acute episode).

We will consider any study regardless of the method used to establish the diagnosis.

Comorbidities

We will include participants with any comorbid psychiatric or physical disorder.

Setting

We will include studies conducted in all settings.

Where studies include subsets of eligible participants, we will only include the study provided separate data is available, either in the study report of through contact with the authors, from the eligible section of the study population.

Types of interventions

Experimental intervention

ECT, meaning the application of electricity to the scalp in order to induce a generalised tonic‐clonic seizure.

We will consider both modified ECT (i.e. ECT applied under general anaesthesia and with administration of a muscle relaxant drug) and unmodified ECT (i.e. ECT applied without anaesthesia). For modified ECT, we will include studies using any anaesthetic and muscle relaxant.

We will consider ECT delivered with any pulse‐width (e.g. sine‐wave, brief‐pulse or ultrabrief‐pulse), electrode placement (e.g. bitemporal, bifrontal, right unilateral) and stimulus dose (e.g. measured as milicoulombs of charge or the dose relative to the dose corresponding to the seizure threshold).

We will consider any treatment schedule (e.g. once or twice weekly) or duration of the treatment course (i.e. the number of times ECT was administered during the treatment course).

Comparator intervention

We will include the following comparators:

• sham ECT (i.e. a procedure similar to ECT, involving anaesthesia, with or without muscle relaxant, but without delivery of electricity);

• pharmacological treatment, including, but not limited to, antidepressants, antipsychotics, anticonvulsants and lithium;

• non‐pharmacological treatment, including, but not limited to, interventions such as psychotherapy, social interventions and other types of brain stimulation (e.g. rTMS); and

• no intervention.

Co‐interventions

We will include studies regardless of whether ECT was administered as monotherapy, in combination with non‐pharmaceutical or pharmaceutical intervention or as augmentation of another non‐pharmaceutical or pharmaceutical intervention.

Types of outcome measures

We will apply a hybrid approach as specified in Chapter 19 of the Cochrane Handbook for Systematic Reviews of Interventions (Peryer 2019), combining both confirmatory and exploratory approaches to capture both anticipated and previously unrecognised adverse effects of ECT.

Primary outcomes

• Mortality assessed as the number of deaths for any reason

• Retrograde amnesia, including autobiographical information, measured using any relevant instrument (e.g. the Columbia University Autobiographical Memory Interview (CUAMI) (McElhiney 1995), the CUAMI short form (CUAMI‐SF) (McElhiney 2001), an altered version of the CUAMI (Semkovska 2012) or the Kopelman Autobiographical Memory Interview (Kopelman AMI) (Kopelman 1989)

Secondary outcomes

• Serious adverse events, defined as the number of participants with at least one medical events that is life threatening, results in death, disability or significant loss of function, causes hospital admission or prolonged hospitalisation (EMA 2002)

• Adverse events, defined as the number of participants with at least one adverse event. We will categorise adverse events at the System Organ Class and Preferred Term level according to the Medical Dictionary for Regulatory Activities terminology (MedDRA) (MedDRA 2021)

• Adverse events, defined as the number of adverse events, categorised as above

• Treatment emergent hypomanic, manic, depressive or mixed episodes, depending on the participant population

• Self‐reported cognitive deficits, such as assessed using the Cognitive Failures Questionnaire (Broadbent 1982) or any other relevant instrument

Reporting one or more of the outcomes listed here in the trial is not an inclusion criterion for the review. Where a published report does not report one of these outcomes, we will access the trial protocol and contact the trial authors to ascertain whether the outcomes were measured but not reported. Relevant trials that measured these outcomes but did not report the data at all, or did not report it in a usable format, will be included in the review as part of the narrative analysis.

Timing of outcome assessment

We will extract outcomes post‐intervention (i.e. at the end of the treatment period) at the time points reported in the studies and group them into short‐term (one to eight weeks) and long‐term (longer than eight weeks).

As guidelines generally recommend that treatment consists of six to 12 ECT treatments and generally are administered two to three times per week (Lisanby 2007; RANZCP 2019; WFSBP 2013), we will consider the time period of one to eight weeks for our primary analysis. Where a study reports an outcome at more than one time point within one of the prespecified time periods, we will select the latest time point available. We will also extract outcomes measured post‐treatment (i.e. after the end of the treatment period) as some harms may only become apparent long after starting ECT while others may subside or diminish; we will categorise these outcomes as short term (up to six months post‐treatment) and long term (longer than 12 months post‐treatment). We recognise that such outcomes can be biased due to differences arising between groups in the treatment and care received after the treatment period and will discuss the results accordingly. 

Hierarchy of outcome measures

If studies report multiple measures of an eligible outcome, we will include the data based on several considerations. If several measures of an outcome are available on the same hierarchy level used in a study, we will prioritise the outcome measures according to the order specified for each of the outcomes above. If several outcome measures on the same scale are available (e.g. instruments for measuring retrograde amnesia), we will give priority to the outcome measure that is most frequently used across all the included studies. If several analyses are available, we will give priority to an adjusted model (e.g. adjustment for baseline measures of the outcome or other confounders), if appropriately conducted, and use the effect estimates directly. If multiple adjusted estimates are available for a result, we will prioritise the one judged to minimise the risk of bias due to confounding the most (Reeves 2019). 

Search methods for identification of studies

Electronic searches

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

• Cochrane Common Mental Disorders Controlled Trials Register (CCMDCTR) (all available years);

• Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library;

• Ovid MEDLINE (1946 onwards) (Appendix 1);

• Ovid Embase (1974 onwards);

• Ovid PsycINFO (1806 onwards);

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov/; all available years);

• World Health Organization International Clinical Trials Registry Platform (apps.who.int/trialsearch/; all available years).

Additionally, we will search regulatory data from the US Food and Drug Administration (FDA) (www.fda.gov).

Searching other resources

We will check reference lists of all included studies, relevant books and any relevant systematic reviews identified for additional references to trials. We will also examine any relevant retraction statements and errata for the included studies. We will also conduct internet searches for relevant grey literature sources such as reports, dissertations, theses, databases and databases of conference abstracts.

We will contact all study authors to obtain the study protocol, if this is not otherwise available, and any data or information needed in order to assess eligibility, calculate effect sizes, assess unreported outcomes and perform 'Risk of bias' assessments.

Data collection and analysis

Selection of studies

Two review authors (KM and ASP‐M) will independently screen titles and abstracts for inclusion of all the potential studies we identify as a result of the search and code them as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. If there are any disagreements, we will seek to resolve the issue through discussion and, if necessary, a third review author (KJJ) will be asked to arbitrate. We will retrieve the full‐text study reports of potentially eligible studies. Two review authors (KM and ASP‐M) will independently screen the full‐text and identify studies for inclusion, and identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion or, if required, or by consulting a third review author (KJJ). We will identify and exclude duplicates and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009) and a 'Characteristics of excluded studies' table.

Data extraction and management

We will use an electronic data collection form for study characteristics and outcome data piloted on at least one study included in the review. Two review authors (KM and ASP‐M) will independently extract data from the included studies. We will resolve disagreements by consensus or by involving a third review author (KJJ). We will extract the following study characteristics and outcome data.

• Methods: study design, intervention allocation method, total duration of study, duration of follow‐up, details of any 'run in' period, number of study centres and location, study setting, and date of study start and completion.

• Participants: N randomized, N lost to follow‐up/withdrawn with reasons, N analysed for each outcome, mean age, age range, sex, diagnostic criteria used to establish the diagnosis, N having previously received ECT, inclusion criteria, and exclusion criteria.

• Interventions: intervention, comparison, concomitant medications or non‐pharmaceutical treatment, ECT device manufacturer, anaesthetic administered, muscle relaxant administered, pulse width, electrode placement, stimulus current dose, frequency of ECT administration (N times per week), N total ECT delivered, whether rescue medication was allowed in study and if so, number of participants using rescue medication.

• Outcomes: outcomes specified and collected, adjusted intervention effects, and time points reported, any frequency threshold for reporting of adverse events used, whether adverse events were actively monitored (pre‐specified) or spontaneously reported.

• Notes: funding for the trial, and notable conflicts of interest of authors.

We will not extract outcome data as 'zero' unless it is clearly described as such in the study report. Thus, if an adverse event of interest was not explicitly mentioned in the report, we will record it as not reported, rather than assume that the adverse event was not observed. Where an adverse event is specifically mentioned in the report to be "zero," we will check the protocol or methods section of the report for details on the rigour of monitoring. We will record reasons for reaching a decision of a "zero" event. We will also not consider 'withdrawals due to adverse events', commonly reported in trials, as a marker for adverse or severe adverse events (Peryer 2019). 

One review author (KM) will import the data into R (R Core Team 2019). We will double‐check that data is entered correctly by comparing the data presented in the systematic review with the data extraction form.

Assessment of risk of bias in included studies

Two review authors (KM and ASP‐M) will independently assess the risk of bias for each study using version two of the Cochrane 'Risk of bias' tool (RoB 2) for randomised trials and the Cochrane 'Risk of bias in non‐randomised studies of interventions (ROBINS‐I)' tool for non‐randomised studies, as outlined in the Cochrane Handbook (Higgins 2019a; Sterne 2019). We plan to use the RoB2 and ROBINS‐I Microsoft Excel tools, respectively, available at the RoB2 website to manage the assessment of risk of bias. We will resolve any disagreements by discussion or by involving another review author (KJJ). 

We will assess the risk of bias of a specific result of randomised trials according to the following 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 will assess the risk of bias of a specific result of cluster‐randomised trials using the Cochrane RoB 2 tool for cluster‐randomised trials, as outlined in Chapter 8 of the Cochrane Handbook (Higgins 2019a).

We will use the signalling questions in the RoB 2 tool and rate each domain as 'low risk of bias', 'some concerns' or 'high risk of bias'. We will summarise the risk of bias judgements across different studies for each of the domains listed for each outcome. The overall risk of bias within the trial for the result is the least favourable assessment across the domains of bias; however, where a trial is judged to have some concerns for multiple domains we will judge the overall risk of bias as high following the approach outlined in Table 8.2.b of the Cochrane Handbook (Higgins 2019a).

We will assess the risk of bias of a specific result of non‐randomised studies according to the following domains:

• bias due to confounding;

• bias in selection of participants into the study;

• bias in classification of interventions;

• bias due to deviations from intended interventions; and bias due to missing data;

• bias in measurement of the outcome; and

• bias in selection of the reported result.

We will use the signalling questions in the ROBINS‐I tool and rate each domain as 'low risk of bias', 'moderate risk of bias', serious risk of bias', 'critical risk of bias', or 'no information'. We will, a priori, consider the following confounding domains when assessing the risk of bias: baseline value of outcome (e.g. measure of retrograde amnesia), medical co‐morbidity, age, sociodemographic status, concomitant drug use. Additional confounding domains considered during the preparation of the review will be reported as part of the risk of bias assessment. We will a priori consider the following co‐interventions when assessing the risk of bias: psychological interventions (e.g. psychotherapy) and other non‐pharmacological interventions (e.g. exercise or lifestyle advice). We will summarise the risk of bias judgements across different studies for each of the domains listed for each outcome.  We will reach an overall risk of bias judgment for within the trial for the result, as the least favourable assessment across the domains of bias, e.g. an overall risk of bias judgement of 'low risk of bias' can be reached only if all domains are judged to be at 'low risk of bias' and a study judged to be at 'critical risk of bias' in at least one domain will reach an overall risk of bias judgment of 'critical risk of bias'. 

We will be aware of special issues in assessing the risk of bias for adverse effects data, such as poor definition, ascertainment, or reporting of harms in included trials, particularly where adverse effects were not pre‐specified and where monitoring and reporting were potentially inadequate (Chou 2010).

We will assess the risk of bias for all outcomes of the included trials that will be included in our 'Summary of findings' tables. For the purposes of this review, we are interested in quantifying the effect of assignment to the interventions at baseline, regardless of whether the interventions are received as intended (the ‘intention‐to‐treat effect’).

We will make our consensus decisions for the signalling questions available as supplemental data stored on the Open Science Framework. Supplemental files will be assigned a digital object identifier (DOI).

Measures of treatment effect

We will analyse dichotomous data as odds ratios (OR) with 95% confidence intervals (CI) and continuous data as mean difference (MD) or, where different scales were used to measure the same outcome, as a standardized mean difference (SMD), with 95% CIs. We will enter data presented as a scale with a consistent direction of effect. If studies report the outcome as both an endpoint score and a baseline to endpoint change score, we will prioritise endpoint scores, as they may be easier to interpret clinically; if these are not available, we will use the change score from baseline to endpoint. If both the mean and standard deviation (SD) for baseline and change from baseline are available, but not endpoint scores, we will transform these data into endpoint means and estimate the endpoint SD using the formulae in Chapter 6 of the Cochrane Handbook (Higgins 2019b). We will not pool data using endpoint scores and baseline‐to‐endpoint change scores when calculating SMDs, for reasons outlined in Chapter 10 of the Cochrane Handbook (Deeks 2019). We will also present results calculated as SMD by re‐expressing the data in units of one or more of the instruments used in the included studies, employing an SD calculated as a weighted average across all intervention groups of all studies that used the instrument.

We will narratively describe skewed data using medians and interquartile ranges.

Unit of analysis issues

Cross‐over trials

For cross‐over studies, we will only consider results for the calculation of summary statistics when it is possible to extract data for the first randomized period.

Cluster‐randomised trials

For cluster‐randomised trials, we will analyse results using the generic inverse‐variance approach and using the effect estimates and standard errors reported in the study provided the analyses appropriately accounted for the cluster design. If these data are not available, we will multiply the standard error of the effect estimate by the square root of the design effect and analyse results using the generic inverse‐variance method (Higgins 2019c).

Studies with multiple treatment groups

For studies with multiple arms, we will combine the treatment arms using the methods outlined in Chapter 6 of the Cochrane Handbook (Higgins 2019b) if they can be regarded as providing subtypes of the same treatment and their effect can therefore be considered similar (e.g. different doses within the range of approved dosages). Where this is not the case, we will treat each arm as a separate group and will divide the sample size of the placebo arm between the treatment arms while leaving the mean and SD unchanged for continuous outcomes and split the events evenly among intervention groups for dichotomous variables.

Dealing with missing data

We will contact investigators or study sponsors in order to verify key study characteristics and obtain missing numerical outcome data when relevant (e.g. when a study is identified as abstract only) and document details regarding the correspondence. Where possible, we will calculate missing SDs using other data from the trial, such as CIs, based on methods outlined in Chapter 6 of the Cochrane Handbook (Higgins 2019b). Where this is not possible, we will report the study narratively and discuss its impact in the overall assessment of results.

Dichotomous outcomes

For participants for whom data is available but were excluded from the analyses because of protocol non‐adherence, we will try obtain the data from the original trial report or by directly contacting trial investigators. Where data cannot be obtained for non‐adherent participants we will apply an intention‐to‐treat (ITT) analysis, in which the total of the excluded participants is added to the denominator and the number with events is added to the numerator of the arm to which they were randomized. We will consider the exclusion of ineligible participants who are mistakenly randomized to be appropriate only if information about ineligibility was available at randomization and those making the decision regarding exclusion were blind to allocation; otherwise, we will treat those participants similarly to non‐adherent participants.

For participants with missing dichotomous outcome data we will follow the methods proposed by Higgins and colleagues (Higgins 2008) to assess the potential impact of missing data on the results. We will conduct an available‐case analysis (ACA) as a reference. For our primary analysis, we will conduct an imputed case analysis (ICA), in which we will impute missing data according to reasons for missingness (ICA‐r). We will specify the categorisation of reasons based on a pilot assessment of the study methods in a few included studies, in advance of seeing the data. We will take the uncertainty of the imputed data into account when calculating standard errors, so that these are not inappropriately reduced, and weight the studies accordingly, using the methods outlined in Higgins 2008. When the primary meta‐analysis suggests an important effect, we will conduct several sensitivity analyses to assess the risk of bias associated with missing participant data. First, we will calculate best‐case and worst‐case scenarios, to provide the most extreme limits on the effect estimates compatible with the data. Next, we will conduct several analyses by selecting informative missing odds ratios (IMORs) for the two groups that cover more realistic situations (Higgins 2008), based on, among other information, information about the reasons for missing data. Lastly, we will evaluate the effects of missing participants on the weights awarded to the studies using the method by Gamble and Hollis (Gamble 2005).

Continuous outcomes

For participants with missing continuous outcome data we will follow the methods proposed by Ebrahim and colleagues (Ebrahim 2013) to assess the potential impact of missing data on the results. The method involves conducting an initial ACA as our primary analysis and subsequent sensitivity analyses in which we will make progressively more stringent assumptions about results in participants with missing data. This allows assessment of the extent that results change with the sensitivity analyses, and, in turn, how risk of bias as a result of missing data may increase. In these analyses, we will assume that the reasons for missing data, and the participants with missing data, were similar across studies. We will use five sources of data reflecting observed mean scores in the participants followed‐up (i.e. the best and worse mean score of the intervention group and control group across included trials, respectively, and the mean score of the control arm of the same trial). We will then use these data in four progressively more stringent imputation strategies (Ebrahim 2013). For trials in which authors do not report missing participant data rates, we will use the median missing participant data rate from the remaining trials and perform a sensitivity analysis using a missing participant data rate of zero in both arms. If only the total missing participant data is reported, we will assume that missing data was equally distributed in both arms. If the individual trial handled missing participant data and reported imputed analyses only, we will use the imputed results for the meta‐analysis (Ebrahim 2013). If the authors reported both the imputed analysis and the complete case analysis, we will apply our approach to the trial’s ACA. When different measures were used across trials for assessing the same outcome, we will choose a reference measurement instrument and convert the scores from different instruments to the units of the reference instrument (Ebrahim 2014).

Assessment of heterogeneity

We will assess heterogeneity by comparing participants, interventions, and outcomes between the included studies. In the case of considerable methodological and clinical heterogeneity, we will not pool the data but will describe them separately and report the clinical diversity of the studies.

We will use the I² statistic to quantify inconsistency among the trials in each analysis. We will also consider the P value from the Chi² test. We will consider an I² estimate equal to or greater than 50% accompanied by a statistically significant Chi² test (P < 0.1) as indication of substantial heterogeneity (Deeks 2019). If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analysis.

We will, additionally, inspect forest plots visually to consider the direction and magnitude of effects and the degree of overlap between CIs.

Provided ten or more non‐randomised studies are available for a result, we will undertake meta‐regression analyses to identify important determinants of heterogeneity, even when studies are considered too heterogenous to combine. We will consider a priori the following design features: whether outcome data were available after only or before and after ECT/comparator, and the method used to control for confounding.

Assessment of reporting biases

We will attempt to retrieve the protocols of the included trials and compare the outcomes in the protocol with those in the published report. If we cannot retrieve the protocol we will compare the outcomes in the methods section of the report with the reported results.

Two review authors (KM and ASP‐M) will independently assess the risk of reporting biases using the preliminary Risk Of Bias due to Missing Evidence (ROB‐ME) tool(ROB‐ME 2020). Disagreements will be resolved through discussion or, if necessary, by involving a third review author (KJJ)

We will construct an outcome matrix following the ROB‐ME guidance and will then assess the within‐study and across‐studies non‐reporting bias using the signalling questions and algorithm outlined in the ROB‐ME tool. 

We will present the assessment of risk of reporting biases in a table along with a brief justification for each judgement. We will display studies with missing results in forest plots. 

If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible small study biases for the primary outcomes. We will also use Egger’s test for funnel plot asymmetry provided we can include 10 or more studies in the meta‐analysis and studies are not similar in size (Egger 1997).

Data synthesis

If the treatments, participants and the underlying clinical question are similar enough for it to be considered meaningful, we will undertake meta‐analyses. As results from non‐randomised studies with different combinations of design features are expected to differ systematically, resulting in increased heterogeneity, we will not combine results from non‐randomised studies and randomized trials, or non‐randomised studies with considerably different design features, in a meta‐analysis (Reeves 2019). If the studies are not sufficiently similar to combine in a meta‐analysis, we will display the results of included studies in a forest plot but supressing the summary estimate and will use a narrative synthesis to report the findings of the studies. Since we expect that there will be heterogeneity among studies, we will use the random‐effects model for pooling studies, regardless of the degree of statistical heterogeneity. We will use the Hartung‐Knapp‐Sidik‐Jonkman method for estimating the between‐study variance, as it results in more adequate type I error rates than the often‐used DerSimonian and Laird approach, especially in situations when the number of studies is small (IntHout 2014; Langan 2018); as we expect this be will the case. For dichotomous outcomes where a high proportion of the studies in the meta‐analysis report no events in one or more study arms, we will consider other methods (Deeks 2019; Efthimiou 2018). Where event rates are below 1%, the groups are balanced and the effects are small, we will employ Peto's method; if these conditions are not met, we will employ the Mantel‐Haenszel odds ratio method without continuity correction (Deeks 2019). We will conduct sensitivity analyses using a range of alternative models to assess the robustness of the results, using Peto's method, the Mantel‐Haenszel odds ratio with and without continuity correction, inverse‐variance odds ratio with continuity correction and arcsine difference (Rucker 2009).

Additionally, we will calculate the prediction interval to provide a better appreciation of the uncertainty around the effect estimate (Borenstein 2017), which may be particularly relevant when the between‐study heterogeneity is high (IntHout 2014). As prediction intervals are strongly based on the assumption of a normal distribution for the effects across studies, and can therefore be problematic when the number of studies is small, we will only calculate them provided there are 10 or more studies and no clear funnel plot asymmetry.

For the primary analysis of randomised trials, we will include all eligible trials regardless of their risk of bias. We will explore the influence of including studies judged as 'high risk' of bias or as 'some concerns' in sensitivity analyses. For the primary analysis of non‐randomised studies, we will exclude eligible studies that are judged to be at critical risk of bias and will explore the influence of including studies judged as at 'serious risk of bias' in sensitivity analyses.

All analyses will be performed using the freely available software R (R Core Team 2019).

Main comparison

We will make the following main comparisons.

• ECT versus sham‐ECT.

• ECT versus pharmacological treatment.

• ECT versus non‐pharmacological treatment.

• ECT versus no treatment.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses for any outcomes with substantial heterogeneity.

• Approach for ascertainment of adverse effects. Studies that employ active monitoring or surveillance are more likely to identify adverse events than studies relying on spontaneous report monitoring. We will categorise studies according to whether the outcome was ascertained using a confirmatory approach or an exploratory approach.

• Treatment schedule. Observational evidence indicates that the effect of ECT and cognitive adverse effects are moderated by the frequency with which the treatment is administered (Gangadhar 2010). We will assess the impact of the mean number of administrations of ECT per week in meta‐regression.

• Age of participants. Due to differences in brain development between children and adolescents, and adults, the adverse effects of ECT may be different in children and adolescents compared with adult and elderly patients.We will categorise the studies according to whether the mean age of the participants was below 18 years, older than 18 years and below 65 years, and 65 years and older.

• Method of delivery of ECT. Unmodified ECT, compared with unmodified ECT, may be associated with increased risk of adverse events such as broken teeth, joint dislocation and bone fracture (Andrade 2012). We will categorise the studies according to whether they used modified or unmodified ECT.

• Electrode placement and pulse width. Observational evidence indicates that electrode placement and pulse width moderate the effect of ECT and the risk of adverse events, particularly cognitive adverse effects (Lisanby 2007). We will categorise studies according to the stimulation method (e.g. brief‐pulse bilateral ECT, ultra‐brief pulse right unilateral ECT).

Any additional analysis will be reported as post‐hoc. We will compare subgroups using a formal statistical test for subgroup differences. We will undertake subgroup analysis provided ten or more studies are available for each characteristic modelled and covariates are reasonably evenly distributed across studies. Given the risk of type I errors due to multiple testing issues, we will interpret findings from subgroup analysis conservatively.

Sensitivity analysis

We plan to carry out the following sensitivity analyses, to test whether key methodological factors or decisions affected the main result:

• Imputation of missing data using any method. We will analyze the impact of imputing data as described in Dealing with missing data.

• The influence of imputing SDs. We will remove studies for which we have imputed missing SDs based on the SDs of similar studies.

• Risk of bias. We will remove studies for which we have judged the overall risk of bias as 'some concerns' or 'high risk' (for randomised trials) and 'serious risk' (non‐randomised studies).

• Statistical methods for summarising rare dichotomous outcomes. We will perform meta‐analysis using different methods for pooling studies when assessing rare outcomes as described in Data synthesis.

Summary of findings and assessment of the certainty of the evidence

We will create a 'Summary of findings' table using the following outcomes:

• overall mortality;

• retrograde amnesia;

• serious adverse events;

• the number of adverse events;

• the number of patients with at least one adverse event;

• treatment‐emergent affective episodes.

We will prioritise the presentation of outcomes assessed at one to eight weeks. We will use the five GRADE considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of a body of evidence as it relates to the studies which contribute data to the meta‐analyses for the prespecified outcomes. We will use methods and recommendations described in Chapter 14 of the Cochrane Handbook (Schunemann 2019). We will use the GRADEpro software (GRADEpro GDT 2015). We will use the 'overall risk of bias' across studies to inform our GRADE judgements for each outcome. Each comparison (ECT versus sham ECT, ECT versus pharmacological treatment, ECT versus non‐pharmacological treatment and ECT versus no treatment) will be displayed in a separate 'Summary of findings' table. If both randomised trials and non‐randomised studies are available for a result, we will present results for randomised trials and non‐randomised studies separately. We will justify all decisions to downgrade the certainty of the evidence using footnotes and where necessary, we will make comments to aid readers' understanding of the review.

Judgements about the certainty of the evidence will be made by two review authors (KM and ASP‐M) working independently, with disagreements resolved by discussion or involving a third review author (KJJ). Judgements will be justified, documented and incorporated into reporting of results for each outcome.

Reaching conclusions

We will base our conclusions only on findings from the quantitative or narrative synthesis of included studies for this review. We will avoid making recommendations for practice and our implications for research will suggest priorities for future research and outline what the remaining uncertainties are in the area.

Appendices

Appendix 1. MEDLINE ‐ Adverse Events Search

Ovid MEDLINE(R) <1946 to September 30, 2021>
1 *Electroconvulsive Therapy/ae, co, mo [Adverse Effects, Complications, Mortality] 1203

2 ((ECT or electroconvuls* or electr* convuls* or electroshock* or electr* shock*) and (adverse or side effect* or treatment emergent or undesirable effect* or complication* or contraindicat* or safety or tolerability or tolerance or tolerat* or harm or harms or harmful or injur* or damage* or impair* or risk or risks or death? or mortalit* or suicid*)).ti,kf. 1089

3 (((ECT or electroconvuls* or electr* convuls* or electroshock* or electr* shock*) adj5 (adverse or side effect* or treatment emergent or undesirable effect* or complication* or contraindicat* or safety or tolerability or tolerance or tolerat* or harm or harms or harmful or injur* or damage* or impair* or risk or risks or death? or mortalit* or suicid*)) and (intervention? or treatment? or therap*)).ab. 1389

4 ((ECT or electroconvuls* or electr* convuls* or electroshock* or electr* shock*) and (memory loss or brain damage)).mp. 228

5 ((ECT or electroconvuls* or electr* convuls* or electroshock* or electr* shock*) adj5 (apathy or agitat* or restless* or confus* or concentrat* or loss or memor* or emotional response?)).ti,ab,kf. 708

6 or/1‐5 3455

7 treatment outcome/ or treatment failure/ 1095903

8 case‐control studies/ or cohort studies/ or follow‐up studies/ or exp longitudinal studies/ or prospective studies/ or retrospective studies/ or controlled before‐after studies/ or cross‐sectional studies/ or historically controlled study/ 2780674

9 (registry or registries or regist* based).ti,ab,kf,hw. 190463

10 ((association or epidemiologic or prospective or retrospective or cross‐sectional or case control* or cohort or longitudinal or observational) adj3 study).ti,ab,kf. 1193901

11 (case? adj (series or crossover or cross‐over)).ti,ab,kf,hw. 87264

12 (case control* or cross‐sectional or cohort? or follow‐up or followup or longitudinal or prospective or retrospective or observational or population).ti. 810962

13 ((cohort? adj3 (analys* or compar* or data or study or studies or trial or randomi#ed or RCT)) or (population adj2 (based or data* or study or studies or register? or registry or registries or survey? or surveillance))).ti,ab,kf. 546084

14 ((compar* adj3 (study or risk?)) and population).ti,ab,kf. 38154

15 ((chart? adj (audit? or review?)) or ((autopsy or hospital* or medical or electronic health) adj2 (report? or record?)) or death certificate?).ti,ab,kf. 213882

16 or/7‐15 4289246

17 6 and 16 901

18 randomized controlled trial.pt. 548931

19 controlled clinical trial.pt. 94499

20 double‐blind method/ or random allocation/ or single‐blind method/ 293813

21 (randomized or randomised or randomly).mp. 1167619

22 (RCT or "at random" or (random* adj3 (administ* or allocat* or assign* or class* or cluster or crossover or cross‐over or control* or determine* or divide* or division or distribut* or expose* or fashion or number* or place* or pragmatic or quasi or recruit* or split or subsitut* or treat*))).ti,ab,kf. 618580

23 (placebo or sham or simulat*).mp. 1033793

24 ((single or double or triple or treble) adj2 (blind* or mask* or dummy)).ti,ab,kf. 182843

25 trial.ti,ab,kf. 662935

26 (control* and (trial? or study or studies or group*)).mp. 3904709

27 or/18‐26 5078929

28 6 and 27 789

29 meta‐analysis/ or "systematic review"/ 245083

30 (systematic or structured or evidence or trials or studies).ti. and ((review or overview or look or examination or update* or summary).ti. or review.pt.) 251471

31 (0266‐4623 or 1469‐493X or 1366‐5278 or 1530‐440X or 2046‐4053).is. 19838

32 meta-analysis.pt. or (meta‐analys* or meta analys* or metaanalys* or meta synth* or meta‐synth* or metasynth*).ti,ab,kf,hw. 240402

33 ((systematic or meta) adj2 (analys* or review)).ti,kf. or ((systematic* or quantitativ* or methodologic*) adj5 (review* or overview*)).ti,ab,kf,sh. or (quantitativ$ adj5 synthesis$).ti,ab,kf,hw. 322671

34 (integrative research review* or research integration).tw. or scoping review?.ti,kf. or (review.ti,kf,pt. and (trials as topic or studies as topic).hw.) or (evidence adj3 review*).ti,ab,kf. 213341

35 review.pt. and ((medline or medlars or embase or pubmed or scisearch or psychinfo or psycinfo or psychlit or psyclit or cinahl or electronic database* or bibliographic database* or computeri#ed database* or online database* or pooling or pooled or mantel haenszel or peto or dersimonian or der simonian or fixed effect or ((hand adj2 search*) or (manual* adj2 search*))).tw,hw. or (retraction of publication or retracted publication).pt.) 170381

36 or/29‐35 643365

37 6 and 36 193

38 17 or 28 or 37 1431

39 exp animals/ not humans.sh. 4907997

40 (38 not 39) 1314

Contributions of authors

Klaus Munkholm: conceptualisation; methodology; writing ‐ original draft; writing ‐ review and editing; supervision.

Karsten Juhl Jørgensen: methodology; writing ‐ review and editing.

Asger Sand Paludan‐Müller: methodology; writing ‐ review and editing.

Sources of support

Internal sources

• Cochrane Denmark, Denmark

  This project was supported by Cochrane Denmark. 

External sources

• National Institute for Health Research (NIHR), UK

  This project was supported by the NIHR, via Cochrane Infrastructure funding to the Common Mental Disorders Group. 

Declarations of interest

Klaus Munkholm: no conflicts of interest.

Karsten Juhl Jørgensen: no conflicts of interest.

Asger Sand Paludan‐Müller: no conflicts of interest.

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