褪黑激素用于提升重症监护室患者睡眠质量
Abstract
研究背景
重症监护病房（ICU）的患者常由于周围环境的影响而导致睡眠中断，如高噪音水平和24小时照明，以及增多的病患护理和侵入性护理操作。睡眠不足会影响身体和心理健康，在ICU的患者通常睡眠质量很差。在 ICU 夜间时间内人工照明可能会减少危重患者的褪黑素产生。众所周知，褪黑激素对昼夜节律有直接影响，它表现出可以重置自然节律从而促进睡眠。
研究目的
目的是评估褪黑激素能否改善ICU的成人患者的睡眠质量和时间。评估为促进睡眠而提供的褪黑激素是否改善了患者的生理和心理结局。
检索策略
我们检索了Cochrane对照试验中心注册库（CENTRAL; 2017年，第8期），MEDLINE（1946年至2017年9月），Embase（1974年至2017年9月），护理和联合健康文献累积索引（CINAHL）（1937年至2017年9月）和PsycINFO（1806至2017年9月）。我们检索了临床试验注册库正在进行的研究，对相关文章进行前后向引文检索。
标准/纳入排除标准
我们纳入了随机和半随机对照试验，纳入对象为不论何诊断的年龄大于16岁的ICU成人患者，接受褪黑素或其他对比剂用于促进睡眠。我们纳入了存在有机械通气的患者和没有存在机械通气的患者。我们计划纳入使用合适临床剂量的褪黑素用于促进睡眠的研究，与安慰剂或其他促睡眠药物进行比较。
数据收集与分析
两位综述作者独立评估了研究结果、提取数据、评估偏倚风险和合并结果。我们使用GRADE评价证据质量。
主要结果
我们纳入了4项研究共计151名随机受试者。两项研究纳入机械通气患者，一项研究同时纳入了机械通气和非机械通气患者，还有一项只纳入了机械通气患者。三项研究报告了入院诊断， 诊断各不同，包括脓毒症、肺炎和心脏或心肺骤停。所有的研究都是比较褪黑素与无活性安慰剂，其中三项研究为安慰剂对照试验，一项研究为褪黑素与常规护理比较。所有的研究都在夜间给予褪黑素。
所有的研究都报告了适当的随机化方法，安慰剂对照试验在受试者和研究人员层面都使用了盲法。我们注意到在一项研究中存在很高的偏倚风险，而两项研究中的潜在偏倚风险不明确，因为受试者的基线水平存在差异。
由于测量工具的差异和报告数据的方式不同，无法进行数据合并。
褪黑素对主观的睡眠质量和时间的改善并不明确（非常低的确定性证据）。三项研究的139 名受试者通过受试者自己或家庭成员衡量睡眠时间和质量。一项研究的作者报告了受试者自己评估（使用Richards‐Campbell睡眠问卷表）和护士评估睡眠效率指数在组间没有差异。两项研究报告说护士观察到的睡眠时间长短在组间无差异。
褪黑素对客观的睡眠质量和时间的改善并不明确（非常低的确定性证据）。两项研究（37 名受试者）使用多导睡眠记录仪、活动记录仪、双频指数、脑电图来测量睡眠的质量和睡眠时间。一项研究作者报告了使用双频指数和活动记录仪来评估睡眠效率指数，组间没有差异。这些研究者还报告了给予褪黑激素的受试者的睡眠时间较长，在统计学上没有统计学意义，并且通过对BIS数据的曲线下面积（AUC）的分析，给予褪黑激素的受试者睡眠改善（被称为“更好的睡眠”）。 一项研究使用了多导睡眠图测量睡眠情况，但由于受试者数据的大量丢失而无法报告数据。
一项研究（82 名受试者）报告称没有证据表明组间焦虑评分有差异（非常低的确定性证据）。两项研究（94 名参与者）报告了死亡率数据：一项研究报告说有三分之一的受试者死亡；另一项研究报告说，没有证据表明不同组间的医院死亡率存在差异（非常低的确定性）。一项研究（82 名参与者）报告称没有证据表明组间住ICU的时间有差异（非常低的确定性证据）。两项研究（107 名参与者）中报告了褪黑激素尚不明确（非常低确定性证据）的不良反应 ： 一项研究报告说在给予褪黑素后一位受试者出现了头痛，另一项研究报告说，给予褪黑素后一位受试者出现了嗜睡，在对照组也发生了两个不良事件（一位受试者出现了皮肤反应，另一位受试者出现过度嗜睡）。
由于受试者人数少数据有限，每项研究结果的证据都都缺乏确定性。我们注意到在一些研究中由于基线数据的高度丢失和组间差异，本研究具有一定局限性，并且不同研究给予的褪黑素剂量也各不相同。用于测量数据结果的方法不一致，某些测量工具可能并不适用于ICU患者。 所有研究的受试者都是来自ICU，但我们注意到不同ICU的临床路径有差异，其中一项研究使用了非标准镇静流程，这给证据引入了间接性。
作者结论
我们没有发现足够的证据来确定使用褪黑素是否会改善ICU成人患者的睡眠质量和时间。我们提取了很少的数据，并发现各研究的方法、ICU 镇静规程、 以及用于测量和报告睡眠的方法存在差异。我们在数据库和临床试验注册平台中发现了五项正在进行的研究。未来将这些研究纳入到我们的综述当中，以进一步明确本综述的结论。
PICO
Plain language summary
褪黑激素用于改善重症监护室患者的睡眠
研究背景
ICU患者的睡眠质量通常较差。这可能是由于ICU环境里持续的高水平噪音和24小时持续照明，以及增多的和侵入性的临床护理工作（如测量血压、脉搏、体温、血液标本采集、指导用药等）。睡眠不足会影响一个人的身体和心理健康。人们普遍认为睡眠是健康的基本要求。睡眠具有恢复性功能。对于危重患者，睡眠被认为可以改善预后和提高生存率。在重症监护病房的患者，通常睡眠质量不佳。褪黑激素是人体内产生的一种用于调节睡眠和觉醒周期的荷尔蒙。ICU夜间的人工光可能会影响人体自然产生褪黑素，这可能会影响危重病人的睡眠周期。
综述问题
目的是评估褪黑激素是否能改善 ICU 成人患者的睡眠质量和时间，从而改善患者身心健康。
研究特点
证据截至2017年9月。本综述纳入4项研究，共涉及151位受试者。所有受试者都是住在ICU的重症患者。所有的研究都是比较褪黑素与非活性安慰剂或常规的护理。
主要结果
我们没有将四项研究的数据合并起来。 三项研究由护士和受试者对睡眠进行评估，并报告在睡眠质量和数量上没有差异。 两项研究使用设备来测量睡眠的质量和时间，其中一项研究报告褪黑素的使用在睡眠效率方面没有差异（人在夜间时间睡得多好），根据一些分析显示那些使用了褪黑素的患者有更好的睡眠。一项研究报告设备出现了问题，导致数据丢失。一项研究报告了ICU患者的焦虑状况、死亡率、住ICU时间没有存在差异。我们注意到褪黑素的潜在副作用很少（一位受试者出现头疼，另一位受试者过度嗜睡）。
证据质量
我们注意到不同组的患者服用褪黑素的剂量存在差异。 两项研究报告了不同组患者的个体差异可能会影响到结果。一项研究有大量的数据丢失，另一项研究没有使用标准麻醉药物镇静患者。很少有研究使用合适的仪器来测量睡眠质量。我们发现很少有研究人员评估我们的综述结局。我们发现所有的证据等级都非常的低，因此我们无法确认褪黑素能否改善ICU成人患者的睡眠质量和时间。我们在数据库和临床试验注册平台中发现了五项正在进行的研究。未来将这些研究纳入到我们的综述当中，以进一步明确本综述的结论。
Authors' conclusions
Summary of findings
| Melatonin compared with no agent for the promotion of sleep in adult patients in the ICU | ||||
| Patient or population: adult patients in the ICU Settings: ICUs, in Australia, Italy, UK, and US Intervention: melatonin Comparison: no agent | ||||
| Outcomes | Impacts | No of participants | Quality of the evidence | Comments |
| Quantity and quality of sleep as measured through reports of participants or of family members or by personnel assessments Data collected at end of follow‐up | In 1 study, participants completed the RCSQ and study authors reported no difference in SEI scores between groups. This was consistent with nurse assessment for which study authors also reported no difference in SEI scores between groups 2 studies reported no difference in duration of sleep observed by nurses | 139 (3 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies used different methods to report data |
| Quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG Data collected at end of follow‐up | In 1 study, investigators used BIS and actigraphy to record sleep. Study authors reported no difference in SEI scores with both tools. Study authors also reported longer sleep in participants given melatonin which was not statistically significantly different, and also reported evidence of improved sleep in participants given melatonin from analysis of AUC using BIS data 1 study used PSG, with a large loss of participant data at follow‐up, which prevented analysis of sleep data | 37 (2 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies differed in types of measurement tools |
| Anxiety or depression, or both Data collected at end of follow‐up | 1 study (using VNR ≥ 3) reported no evidence of a difference in anxiety scores between groups | 82 (1 study) | ⊕⊝⊝⊝ | We identified only one study and could not conduct meta‐analysis |
| Mortality Study authors did not report final timepoint for data collection. | 1 study reported one‐third of participants had died; number of deaths per group was not reported 1 study reported no evidence of a difference between groups in hospital mortality | 94 (2 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies different in methods of reporting data |
| Length of stay in the ICU | One study reported no evidence of a difference in length of ICU stay between groups | 82 (1 study) | ⊕⊝⊝⊝ | We identified only 1 study and could not conduct meta‐analysis |
| Adverse events (such as nausea, dizziness and headache) Data collected at end of follow‐up | 1 study reported headache in one participant who was given melatonin 1 study reported a cutaneous rash in one participant in the control group, and 2 participants (1 participant in both groups) with excessive sleepiness | 107 (2 studies) | ⊕⊝⊝⊝ | We could not conduct meta‐analysis because studies different in reported types of adverse events |
| Acronyms and abbreviations AUC: area under the curve; BIS: bispectral index; EEG: electroencephalogram; ICU: intensive care unit; PSG: polysomnography; RCSQ: Richards‐Campbell Sleep Questionnaire; SEI: sleep efficiency index; VNR: verbal numeric range | ||||
| GRADE Working Group Grades of Evidence | ||||
| aWe downgraded by 2 levels for imprecision; there were few studies with few participants, and outcome measures included both personnel and participant reports. We downgraded by 1 level for study limitations; we noted differences in baseline characteristics in two studies which may have influenced results. We downgraded by 1 level for inconsistency; we noted differences in doses of melatonin given in each study. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in one study were generalizable to most ICUs bWe downgraded by 2 levels for imprecision; there were few studies very few participants, and outcome measures used different assessment tools which may not effectively measure sleep in the ICU patient. We downgraded by 1 level for study limitations; we noted differences in baselines characteristics in one study which may have influenced results. We downgraded 1 level for inconsistency; we noted differences in doses of melatonin given in each study. We downgraded by 1 level for study limitations; we noted high risk of performance bias and high attrition which prevented adequate outcome reporting cWe downgraded by 2 levels for imprecision; data was from one study with few participants, and we could not be certain whether this outcome was measured with an appropriate tool for patients in the ICU. We downgraded by 1 level for study limitations; pre‐treatment use of opiates differed between study groups. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs dWe downgraded by 2 levels for imprecision; there were few studies with few participants. We downgraded by 1 level for study limitations; we noted a high risk of performance bias and attrition bias in one study and we noted differences between groups in pre‐treatment use of opiates. We downgraded 1 level for inconsistency; doses of melatonin varied between studies. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs eWe downgraded by 2 levels for imprecision; data was from one study. We downgraded by 1 level for study limitations; pre‐treatment use of opiates differed between study groups. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs fWe downgraded by 2 levels for imprecision; there were few studies with few participants. We downgraded by 1 level for study limitations; we noted differences in baseline characteristics in two studies which may have influenced results. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs | ||||
Background
This is one of two reviews performed to examine the use of pharmacological agents to promote sleep in the intensive care unit with similar text linked across the reviews (Lewis 2016a).
Description of the condition
It is accepted that sleep is an essential requirement for good health. Sleep has a restorative function, and for the critically ill is thought to improve healing and survival (Tembo 2009).
Sleep naturally follows a circadian rhythm of approximately 24 hours, in a diurnal pattern of once a day. Each period of sleep consists of phases lasting 90 minutes, with typical sleep ‘architecture’ involving a period of rapid eye movement (REM) and non‐rapid eye movement (NREM). The NREM stage is subdivided into three phases, now labelled as N1, N2, and N3 (also described as 'slow wave patterns'). The REM stage accounts for 15% to 20% of sleep time, and N2 of NREM for approximately 50% (Matthews 2011; Schupp 2003; Silber 2007).
It is likely that patients in hospital will be subject to sleep disturbances; this is particularly likely for those in the intensive care unit (ICU). These patients are critically ill with diagnoses such as respiratory insufficiency or failure, need for postoperative management, ischaemic heart disorder, sepsis, and heart failure (Society of Critical Care Medicine). Patients may require specialist support after elective surgery, or may be emergency admissions following medical events or trauma (e.g. with multiple injuries after a road traffic accident) (Intensive Care Foundation).
In the ICU, the ratio of staff to patients is higher than in general wards and the environment typically includes 24‐hour lighting, a constant level of noise, and more frequent patient care activities (measuring blood pressure, pulse, and temperature; taking blood samples; administering medications, etc.) than in general wards. Many patients are mechanically ventilated (up to 40%; Esteban 2000); and are subject to invasive procedures such as tracheal intubation and use of nasogastric tubes (Esteban 2000). In addition, patients in the ICU have critical conditions that involve pain, anxiety, and stress (Kamdar 2012a).
Patients are often prescribed drugs that further contribute to sleep loss. For example, drugs such as benzodiazepines are given for essential sedation (particularly to mechanically ventilated patients) to relieve discomfort and stress. These agents alter sleep architecture so that N2 of NREM is longer than normal, prolonging sleep. However, they also reduce essential REM and N3 phases of sleep (Bourne 2004). Similarly, opioids for analgesia are commonly used in the ICU, and studies report that these agents, even when given in low doses and to healthy volunteers, reduce the amount of deep sleep by up to 50% (Dimsdale 2007; Grounds 2014).
Patients perceive that the quality of their sleep in the ICU is disrupted by frequent awakenings and increased daytime sleep (Freedman 1999). This perception is supported by trials that assessed sleep by using objective measures. Polysomnography readings, which use a variety of channels to measure electrical activity of the heart, as well as muscle tension, airflow and eye movement, can be used to assess sleep. Patients in the ICU have been shown to have alterations to their circadian rhythm, with up to 50% of sleep occurring during the day, and with sleep arousals occurring as often as 39 times per hour in mechanically ventilated patients (Parthasarathy 2004). Changes to sleep ‘architecture’ are significant, with reductions in both REM and N3 sleep (Cooper 2000; Drouot 2008).
Empirical evidence on immediate and long‐term physical consequences of sleep deprivation for patients in the ICU is limited, but data suggest that sleep loss in healthy participants can result in physical alterations to the immune system, as well as changes in metabolism, nitrogen balance, and ventilatory and cardiovascular systems (Kamdar 2012a; Matthews 2011; Pisani 2015; Weinhouse 2006). For example, after loss of only one night's sleep, biomarkers are released that are present in patients with coronary artery disease (Sauvet 2010), although no longitudinal studies have demonstrated that sleep disturbance in the ICU results in increased cardiovascular mortality (Kamdar 2012a). Psychological consequences of sleep loss in healthy participants include depression, anxiety, and stress (Kamdar 2012a); and these symptoms, along with symptoms such as post‐traumatic stress disorder, may be experienced for several months after ICU discharge by survivors of critical illness (Eddleston 2000; Figueroa‐Ramos 2009; Kamdar 2012a; Matthews 2011). However, the association between these long‐term symptoms and sleep disruption during the ICU stay is not known (Kamdar 2012a).
Description of the intervention
Non‐pharmacological interventions, such as noise and light reduction strategies (e.g. earplugs, eyemasks; Richardson 2007), have been studied specifically in the ICU, and some have been shown to improve the quality of sleep. A Cochrane Review has explored the effectiveness of these various strategies (Hu 2015).
This review aims to look at administration of melatonin to adults in the ICU to promote sleep. This molecule is naturally synthesized in the pineal gland during night‐time darkness. It is not stored but is immediately released into the bloodstream and cerebrospinal fluid. Melatonin can be given in tablet, capsule, or liquid form, for immediate or prolonged release. It has few side effects (including headache, dizziness, and nausea); a systematic review found no significant differences in the number of side effects reported when melatonin was used for primary sleep disorders (Buscemi 2005).
How the intervention might work
Artificial lighting during night‐time hours in the ICU may contribute to reduced production of melatonin in critically ill patients. Melatonin is known to have a direct effect on the circadian rhythm and, although it is not a hypnotic agent, it appears to reset a natural rhythm, thus promoting sleep (Reiter 2003). Cochrane Reviews have demonstrated increased length of sleep with melatonin after disruption from shift work (Liira 2014), reduction in preoperative anxiety (Hansen 2015), and reduction in, or prevention of, jet lag (Herxheimer 2002). It is possible that administration of melatonin orally or intravenously to patients in the ICU setting may entrain a circadian rhythm.
Why it is important to do this review
The James Lind Alliance, a priority‐setting organization that works with patients, carers, and clinicians to establish research priorities for health care, recently published its top 10 priorities for research in the intensive care setting (www.jla.nihr.ac.uk/top‐tens/intensive‐care‐top‐10). Among these are research topics relevant to enhancing patient comfort in the ICU (including minimizing pain, discomfort, agitation, and anxiety), preventing physical consequences of critical illness, and providing psychological support for patients.
Although sleep disruption may affect many hospital patients, those in the ICU are particularly vulnerable to disturbances that may subsequently lead to physical and psychological consequences, such as those identified above. No Cochrane Reviews have assessed whether pharmacological agents provide benefit in promoting patient sleep in the ICU, and whether effectively promoting sleep will improve patient outcomes and provide immediate and long‐term clinical benefits. This review will address James Lind Alliance priority targets by assessing the effectiveness of melatonin for sleep promotion in the ICU setting.
Objectives
To assess whether the quantity and quality of sleep may be improved by administration of melatonin to adults in the intensive care unit. To assess whether melatonin given for sleep promotion improves both physical and psychological patient outcomes.
Methods
Criteria for considering studies for this review
Types of studies
We included randomized controlled trials (RCTs) and quasi‐randomized controlled trials (for example, studies in which participants were assigned by alternation, date of birth, or medical record number).
Types of participants
We included adult participants over 16 years of age who were admitted to any ICU as emergency, medical, or postoperative elective surgical patients. We did not limit types of participants by severity of the condition. We included participants who were mechanically ventilated and those who were not mechanically ventilated.
Types of interventions
We included studies that compared the use of melatonin given at an appropriate clinical dose with the intention of promoting night‐time sleep, against:
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no agent; or
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another agent, administered specifically to promote sleep.
Types of outcome measures
We were interested in quantity and quality of sleep. The experience of sleep may not always be representative of objectively measured sleep, and given that patients perceive that they have disrupted sleep while in the ICU (Freedman 1999), we included this outcome, regardless of whether validated scales had been used for measurement. An added issue for this outcome is that critically ill patients may have limited or no ability to communicate. Therefore, we were equally interested in the perceptions of carers and family members who may have an impression of sleep from the bedside, and in subjective measures used by personnel to assess sleep. We included assessments of sleep that have been performed at the end of follow‐up, as defined by study authors, for example in the morning or during the daytime that followed administration of the intervention. We included assessments that were completed with the use of scales, whether validated or not, and modified for each user, such as the Richards‐Campbell Sleep Questionnaire (Richards 2000), or through compilation of sleep diaries, such as the Pittsburgh Sleep Diary (Monk 1994).
Study authors may use scales to determine levels of participant consciousness and we aimed to report study authors' interpretations of these scales. For example, participants may be sedated at level 3 on the Ramsay Sedation Scale (“Patient responds to commands only”) and may be in a sleep‐like state at level 4 or 5 on this scale (“Patient exhibits brisk response to light glabellar tap or loud auditory stimulus” or “Patient exhibits a sluggish response to light glabellar tap or loud auditory stimulus”) (Ramsay Sedation Scale).
We reported the quantity and quality of sleep as measured by objective equipment. In particular, polysomnography (PSG) is considered the most accurate and objective tool that can be used to measure sleep and to identify sleep disorders (Beecroft 2008). PSG measurements can be analysed to detect sleep onset, sleep efficiency, and length of sleep stages, as well as irregularities, such as apnoea and interrupted sleep. We also accepted measurements obtained when other tools had been used to record sleep activity (Beecroft 2008; Benini 2005; Elliott 2013): ‘actigraphy’ is a wristband‐style tool that measures gross motor activity and is analysed to score total sleep time, sleep efficiency, and awakenings; bispectral index (BIS) is typically used to calculate depth of anaesthesia through interpretation of an electroencephalogram (EEG) reading; and measures of EEG alone can be used to interpret electrical brain activity as sleep time. We acknowledge that collection and interpretation of data using objective tools may be problematic in people who are critically ill because manual methods have poor inter‐rater reliability (Ambrogio 2008); people who are critically ill may have various forms of encephalopathy (septic, toxic, or metabolic) or may be treated with intravenous sedatives and these factors may make interpretation of EEG readings more problematic. We used interpretations of these measurements as reported by each study author to define the quantity and quality of sleep.
Our aim was to establish not only whether melatonin improves sleep but whether improvement in sleep leads to better patient outcomes. This was reflected in our secondary outcome measure, which considered potential physical and psychological consequences of sleep loss, although we acknowledge that it may not be possible to ascertain whether a reduction in such events is directly attributable to improved sleep. We assessed physical consequences of sleep loss by collecting data from studies that reported the number of participants who had had an adverse event during follow‐up time, as defined by study authors. We assessed psychological consequences of sleep loss by collecting data from studies that reported the number of participants who had been given a diagnosis of anxiety or depression, or both, by using validated assessment tools during the follow‐up period, as defined by study authors.
Primary outcomes
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Quantity and quality of sleep as measured through reports of participants or family members or by personnel assessments.
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Quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG.
Secondary outcomes
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Anxiety or depression, or both, as measured with the use of validated tools, such as the Hospital Anxiety and Depression Scale (HADS) (Zigmond 1983).
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Mortality at 30 days.
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Length of stay in the ICU.
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Adverse events (such as nausea, headache, or dizziness).
Search methods for identification of studies
Electronic searches
We identified RCTs through literature searching with systematic and sensitive search strategies as outlined in Chapter 6.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We applied no restrictions to language or publication status.
We searched the following databases for relevant trials.
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Cochrane Central Register of Controlled Trials (CENTRAL; 2017, Issue 8) in the Cochrane Library (searched 26 September 2017)
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MEDLINE (Ovid SP, 1946 to 26 September 2017)
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Embase (Ovid SP, 1974 to 26 September 2017)
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Cumulative Index to Nursing and Allied Health Literature (CINAHL) (EBSCO, 1937 to 2 October 2017)
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PsycINFO (EBSCO, 1887 to 2 October 2017)
We developed a subject‐specific search strategy in MEDLINE and used that as the basis for the search strategies in the other listed databases. The search strategy was developed in consultation with the Information Specialist. Search strategies can be found in Appendix 1, Appendix 2, Appendix 3, Appendix 4, and Appendix 5.
We scanned the following trial registries for ongoing and unpublished trials (10 July 2017).
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The World Health Organization International Clinical Trials Registry Platform (WHOICTRP) (apps.who.int/trialsearch/AdvSearch.aspx)
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International Standard Randomised Controlled Trial Number (ISRCTN) (www.isrctn.com/)
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ClinicalTrials.gov (ClinicalTrials.gov)
Searching other resources
We carried out citation searching of identified included studies in Web of Science (apps.webofknowledge.com), and Google Scholar (scholar.google.co.uk), on 13 July 2017 and conducted a search of grey literature through ‘Opengrey’ (www.opengrey.eu), on 13 July 2017. We carried out backward citation searching of key reviews identified from the searches. We contacted study authors of included trials.
Data collection and analysis
Two review authors (Sharon Lewis (SL) and Oliver Schofield‐Robinson (OSR)) independently carried out all data collection and analysis before comparing results and reaching consensus. A third review author (Phil Alderson (PA)) was available to resolve conflicts when necessary.
Selection of studies
We used reference management software to collate search results and to remove duplicates (Endnote).
We used Covidence software to screen results of the search from titles and abstracts, and identified potentially relevant studies by using this information alone (Covidence). We sourced the full texts of all potentially relevant studies, and considered whether they met the inclusion criteria (see Criteria for considering studies for this review). We included abstracts at this stage. However, we planned to include abstracts in the review only if they provided sufficient information, and relevant results that included denominator figures for each intervention or comparison group.
We recorded the number of papers retrieved at each stage, and reported this information using a PRISMA flow chart (Liberati 2009). We reported brief details of closely related papers excluded from the review.
Data extraction and management
We used Covidence software to extract the following data from individual studies.
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Methods ‒ type of study design; setting; dates of study; and funding sources.
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Participants ‒ number of participants randomized to each group; baseline characteristics (to include Acute Physiology and Chronic Health Evaluation (APACHE) II scores; mechanical ventilation status and mode of ventilation; length of time in ICU before study commencement; and concomitant medications).
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Interventions ‒ details of intervention and comparison agents (to include dose and timing).
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Outcomes ‒ review outcomes as measured and reported by study authors (to include types of assessment tools; methods of data synthesis; units of measure; and length of follow‐up).
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Outcome data ‒ results of outcome measures.
We considered the applicability of information from individual studies and the generalizability of data to our intended study population (i.e. the potential for indirectness in our review).
If we identified associated publications from the same study, we created a composite dataset from all eligible publications.
Assessment of risk of bias in included studies
We assessed study quality, study limitations, and extent of potential bias by using the Cochrane 'Risk of bias' tool (Higgins 2011). We considered the following domains.
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Random sequence generation (selection bias).
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Allocation concealment (selection bias).
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Blinding of participants and personnel (performance bias).
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Blinding of outcome assessment (detection bias).
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Incomplete outcome data (attrition bias).
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Selective outcome reporting (reporting bias).
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Other sources of bias ‒ use of concomitant drugs.
Blinding to intervention and control agents may be feasible if agents are prepared in coded containers, for example, by an independent pharmacist; lack of blinding of personnel may introduce risk of bias. Successful blinding of participants to group allocation would be possible and would reduce performance and detection blinding. It is also feasible that outcome assessors could be blinded to group allocation to reduce bias. As participants were critically ill, we anticipated that rates of mortality and withdrawal of consent might be higher in the studies included in this review. Therefore, we paid particular attention to reasons given for losses, whether losses were related to the intervention or to chance alone, and whether losses were comparable between groups. If participants received concomitant medication (e.g. morphine), we considered whether that medication could affect sleep and whether the concomitant medication was comparable between study groups. We planned to address other potential biases in the included studies on an individual basis.
For each domain, two review authors (SL and OSR) used one of three measures — low risk of bias, high risk of bias, or unclear risk of bias — to independently judge whether study authors made sufficient attempts to reduce bias. We recorded this information in the 'Risk of bias' tables and presented a summary 'Risk of bias' figure.
Measures of treatment effect
We planned to report physical consequences of sleep deprivation and mortality as dichotomous data (number of participant events per group). We planned to report psychological consequences of sleep deprivation as dichotomous or continuous data (e.g. number of participant events per group, mean scores per group on a scale measuring anxiety). We anticipated that measures of participant‐reported outcomes might differ for each study, depending on the scales used, as might objective measures of quantity and quality of sleep.
Unit of analysis issues
If multi‐arm studies compared more than one relevant intervention versus a control (e.g. no agent), we planned to include both intervention groups but planned to split the data for the comparison or control group (using a ‘halving’ method), as recommended by Higgins 2011.
Dealing with missing data
During the data extraction stage, we attempted to contact study authors to obtain missing data. We used available case data if necessary, rather than imputed values.
Assessment of heterogeneity
We assessed whether our results showed evidence of inconsistency by considering heterogeneity. We anticipated likely heterogeneity between studies and assessed clinical and methodological heterogeneity by comparing similarities between participants, interventions, and outcomes in our included studies using information collected during the data extraction phase. We planned to complete meta‐analyses only for studies that were clinically and methodologically similar.
We planned to assess statistical heterogeneity by calculating Chi² (with an associated P value) or the I² statistic (with an associated percentage). We planned to use the following cut‐offs as a guide to interpretation of I² values: 0 to 40% is not considered important, 30% to 60% suggests moderate heterogeneity, 50% to 90% suggests substantial heterogeneity, and 75% to 100% shows considerable heterogeneity (Higgins 2011).
As well as looking at statistical results, we planned to consider point estimates and overlap of confidence intervals (CIs). If CIs overlap, then results are more consistent. However, combined studies may show a large consistent effect with significant heterogeneity. Therefore, we planned to interpret heterogeneity with caution (Guyatt 2011b).
Assessment of reporting biases
We attempted to source published protocols for each of our included studies by using clinical trial registers. We planned to compare published protocols with published study results to assess the risk of selective reporting bias.
If we identified sufficient studies (i.e. more than 10 studies) (Higgins 2011), we planned to generate a funnel plot to assess risk of publication bias in the review; an asymmetrical funnel plot may indicate publication of only positive results (Egger 1997).
Data synthesis
We planned to complete meta‐analyses of outcomes if comparable effect measures were available from more than one study, and only when measures of clinical and statistical heterogeneity indicate that pooling of results was appropriate. We planned to use the statistical calculator in Review Manager 5 (Review Manager 2014).
We anticipated that our primary objective of subjective sleep measures would collect data from different sources (participants, carers, and personnel). As some evidence suggests that nurses' assessments of sleep may differ from that of patients' (Kamdar 2012b), we did not combine participant‐, family‐, and personnel‐reported assessments of sleep quality, but reported these separately. In addition, subjective sleep assessment tools may not be comparable between studies. If sleep assessment tools included categories of sleep assessment, such as no sleep, minimal sleep, moderate sleep, and majority sleep, we planned to split the data into dichotomous results by comparing the number of people reporting moderate and majority sleep versus the number reporting minimal and no sleep. We planned to combine data across assessment tools if data could be split into equivalent categories; as this was not feasible, we present a descriptive summary of the results of each study.
Similarly, we anticipated that our primary outcome of objective sleep assessment may use different tools that may not be comparable. Because results were not reported with the same tools and with the same measurements, such as mean score for BIS or mean length of each sleep stage for PSG, we present a descriptive summary of the results of each study.
For dichotomous outcomes, we planned to calculate the odds ratio by using summary data presented for each trial. We planned to use the Mantel‐Haenszel effects model, unless events are extremely rare (one per 1000), in which case we planned to use Peto (Higgins 2011). For continuous outcomes, for example PSG readings, we planned to use mean differences. We planned to use a random‐effects statistical model, which allows for the assumption that included studies may estimate different, but related, intervention effects.
We planned to conduct separate analyses for each comparison type (i.e. melatonin vs no agent; melatonin vs a different dose of the same agent; and melatonin vs a different agent).
We planned to calculate CIs at 95% and use a P value of 0.05 or below to judge whether a result was statistically significant.
We planned to consider whether results of analyses were imprecise by assessing the CI around an effect measure; a wide CI would suggest a higher level of imprecision in results. Inclusion of a small number of studies may also reduce precision (Guyatt 2011a).
Subgroup analysis and investigation of heterogeneity
We planned to assess possible reasons for heterogeneity by performing subgroup analyses. We planned to consider the severity of the condition of participants in each study — participants with a more severe condition may already be subject to increased sleep disruption. Similarly, we planned to consider whether participants have a different outcome according to mechanical ventilation status during the study period. We planned also to consider the age of participants — older people (aged > 65 years) have an altered sleep pattern, which includes increased difficulty falling asleep with more awakenings and shorter total sleep time (Ancoli‐Israel 2009), and therefore data on sleep outcomes may be different for members of this patient group than for younger patients.
In summary, subgroups included:
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severity of the health condition based on APACHE II scores (or comparable severity measures): APACHE II scores less than 25; 25 to 35; greater than 35;
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mechanically ventilated participants versus those not mechanically ventilated;
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participants 65 years of age or older versus participants younger than 65 years; and
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participants in a surgical ICU versus those in a medical ICU.
Sensitivity analysis
We planned to explore potential effects of decisions made as part of the review process as follows.
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We planned to exclude all studies that we judged to be at high or unclear risk of selection bias.
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We planned to conduct meta‐analyses by using the alternate meta‐analytical effects (fixed‐effect or random‐effects) model.
We planned to compare effect estimates from the above results versus effect estimates from the main analyses. We planned to report differences that alter interpretation of effects.
We planned to perform sensitivity analyses on all outcomes.
'Summary of findings' table and GRADE
The GRADE approach incorporates assessment of indirectness, study limitations, inconsistency, publication bias, and imprecision. We used assessments made during our analysis to inform the GRADE process (see Data extraction and management, Assessment of risk of bias in included studies, Assessment of heterogeneity, Assessment of reporting biases, and Data synthesis, respectively). This approach provides an overall measure of how confident we can be that our estimate of effect is correct (Guyatt 2008).
We used the principles of the GRADE system to provide an overall assessment of evidence related to each of the following outcomes.
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Quantity and quality of sleep as measured through reports of participants or of family members or by personnel assessments.
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Quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG.
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Anxiety or depression, or both.
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Mortality.
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Length of stay in the ICU.
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Adverse events (such as nausea, dizziness, and headache).
One review author (SL) used GRADEpro software to create a 'Summary of findings' table for each comparison (GRADEpro GDT); and consensus was reached through discussion with a second author (MWP).
Results
Description of studies
Results of the search
We screened 12,005 titles and abstracts from database searches, results from clinical trial register searches, grey literature searches, and forward and backward citation searches. We carried out full‐text review of 16 articles. We excluded seven studies, and reported details of four of these excluded studies. We identified four eligible studies, and five ongoing studies. See Figure 1.
Study flow diagram
Included studies
We included four parallel design randomized controlled studies with 151 participants (Bourne 2008; Foreman 2015; Ibrahim 2006; Mistraletti 2015). Two studies were described as pilot studies (Foreman 2015; Ibrahim 2006). See Characteristics of included studies.
Study population and setting
The four included studies enrolled adult participants admitted to the intensive care unit (ICU).
Two studies included participants that were mechanically ventilated (Bourne 2008; Mistraletti 2015), one study included both participants that were mechanically ventilated and those not mechanically ventilated (Foreman 2015), and one study included participants who were being weaned from mechanical ventilation. Three studies used the APACHE II (Acute Physiology and Chronic Health Evaluation II) scoring system to classify the severity of participant illness: Bourne 2008 reported a mean (standard deviation (SD)) score in the intervention group of 17.3 (± 3.8) and in the control group of 16.8 (± 3.4); Foreman 2015 reported a mean (SD) score in the intervention group of 13 (± 7) and in the control group of 10 (± 6); and Ibrahim 2006 reported a mean (95% CI) score in the intervention group of 19 (15 to 23) and in the control group of 18 (14 to 23). One study used SAPS II (Simplified Acute Physiology Score II) scoring system to classify severity of participant illness (Mistraletti 2015), and reported a mean (SD) score in the intervention group of 45.7 (± 18.2) and in the control group of 44.1 (± 15.3).
Participant admission diagnoses included severe sepsis, postoperative respiratory failure, or pneumonia (Bourne 2008); acute brain injury, cardiac arrest, or sepsis (Foreman 2015); pneumonia, pancreatic diseases, gastrointestinal diseases, cardiorespiratory arrest, or acute myocardial infarction (Mistraletti 2015). One study did not report admission diagnosis (Ibrahim 2006).
We noted length of time in ICU prior to start of trial, where reported. Bourne 2008 reported median (interquartile range (IQR)) number of days in the intervention group of 16.5 days (11.0 to 19.0) and in the control group 16.5 days (13.0 to 20.5). Ibrahim 2006 reported mean (95% CI) sedation time before start of intervention as 33 hours (17 to 49) in the intervention group and 38 hours (17 to 59) in the control group. Participants in Mistraletti 2015, were randomized on day 3. Study authors in Foreman 2015 did not report this information.
We noted that one study used a ICU sedation protocol that was not standard (Mistraletti 2015).
Interventions and comparators
All studies reported administration of melatonin in the evening to promote sleep. Doses administered were: 10 mg melatonin by enteral feeding at 9 p.m. for four consecutive nights (Bourne 2008); 3 mg melatonin by mouth or by enteral feeding at 8 p.m. for three nights up to a maximum of seven nights (Foreman 2015); 3 mg melatonin by enteral feeding through nasogastric tube at 10 p.m. for a minimum of two days or until ICU discharge (Ibrahim 2006); and 3 mg by enteral feeding at 8 p.m. and 3 mg at midnight daily until ICU discharge (Mistraletti 2015).
Three studies compared melatonin against a placebo (Bourne 2008; Ibrahim 2006; Mistraletti 2015). One study compared melatonin against usual care.
Sources of funding
One study reported no external funding (Mistraletti 2015), one study reported university and small grants funding (Bourne 2008), and two studies did not report funding sources (Foreman 2015; Ibrahim 2006).
Excluded studies
We excluded seven studies from assessment of the full‐texts. See Characteristics of excluded studies.
Bellapart 2016 is an RCT comparing use of melatonin in critically ill patients; this pharmacokinetics study did not administer melatonin with the specific aim of promoting sleep. Huang 2015, is an RCT comparing melatonin with ear plugs and eye masks, and with a placebo; this study recruited healthy volunteers to sleep in simulated ICU environment. Two studies were non‐randomized trials; one study was a pharmacokinetics study of melatonin use (Mistraletti 2010), and one study included a control group that were not in the ICU (Shilo 2000). Three reports were incorrect study designs for our purposes: two were commentaries and one was a literature review (Elliott 2014; Morandi 2015; Owens 2016).
Awaiting classification
We identified no studies awaiting classification.
Ongoing studies
We identified five ongoing studies from clinical trial registers and database searches. Four studies compare evening administration of melatonin with a placebo (ACTRN12610000008022; Huang 2014; Martinez 2017; NCT02615340), and one study compares melatonin with lorazepam (IRCT2015082523760N1). See Characteristics of ongoing studies.
Risk of bias in included studies
See Figure 2 and Figure 3, and Characteristics of included studies.
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study. Blank spaces in figure indicate that outcomes were not reported by study authors, and therefore risk of bias was not completed for these domains.
Allocation
All studies were described as randomized, and provided sufficient details on the method of randomization (Bourne 2008; Foreman 2015; Ibrahim 2006; Mistraletti 2015); we judged these to have low risk of bias.
Two studies provided sufficient details about methods used to conceal allocation from personnel (Ibrahim 2006; Mistraletti 2015); we judged these studies to have a low risk of bias. Two studies provided no details (Bourne 2008; Foreman 2015).
Blinding
Three studies used a placebo formula in the control group (Bourne 2008; Ibrahim 2006; Mistraletti 2015). Bourne 2008 and Ibrahim 2006 reported that personnel and participants were blind to the intervention group and Mistraletti 2015 reported that personnel were blind to the intervention group; we judged these studies to be at low risk of performance bias. It was not feasible to blind personnel or participants in Foreman 2015, which compared melatonin use to usual care, and we judged this study to be at high risk of performance bias.
Three studies reported outcomes that were subjective, and assessed by personnel or participants (Bourne 2008; Ibrahim 2006; Mistraletti 2015). All studies reported blinding for outcome assessment and we judged these to have low risk of detection bias for these outcomes.
Three studies reported outcomes that were objective (Bourne 2008; Foreman 2015; Mistraletti 2015). Two studies reported blinding of personnel and we judged these to have low risk of detection bias (Bourne 2008; Mistraletti 2015). We were unable to judge risk of detection bias for objective outcomes in one study because of lack of reported information (Foreman 2015).
Incomplete outcome data
We judged one study to have low risk of attrition bias, because losses were few and were clearly reported (Mistraletti 2015). There was a large number of losses in Foreman 2015 and we judged this to have a high risk of attrition bias. We judged two studies to have unclear risk of bias because losses were unclearly reported (Bourne 2008; Ibrahim 2006).
Selective reporting
One study had prospective clinical trials registration and we judged this to have low risk of selective reporting bias (Mistraletti 2015). One study had retrospective registration with a clinical trials register, and it was not feasible to judge risk of selective reporting bias using trial registration documents (Bourne 2008); we noted an unclear risk for selective reporting bias. We were unable to source clinical trials registration documents for two studies (Foreman 2015; Ibrahim 2006), and it was not feasible to judge risk of bias; we noted an unclear risk of selective reporting bias.
Other potential sources of bias
Baseline characteristics appeared comparable and we noted no other sources of bias in one study (Ibrahim 2006). Study authors noted some differences in use of opiates between groups in one study (Mistraletti 2010); another study reported differences in some baseline characteristics (age and delirium) and we noted potential differences in ad hoc use of non‐pharmacological methods of sleep promotion (Bourne 2008); and one study was small and not clearly reported (Foreman 2015). We were unable to assess whether these studies had other sources of potential bias.
Effects of interventions
See: Summary of findings for the main comparison
Comparison 1: melatonin versus no agent
Primary outcomes
Quantity and quality of sleep as measured through reports of participants or family members or by personnel assessments
Three studies (139 participants) reported quantity and quality of sleep through participant and personnel assessments. Study authors reported this outcome using different assessments which were not comparable, and we could not combine data in meta‐analysis. See Table 1 for data reported by individual studies.
| Outcome: quantity and quality of sleep as measured through reports of participants or family members or by personnel assessments | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| SEI, patient assessment (RCSQ) | mean (95% CI): 0.41 (0.24 to 0.59); n: 12 | mean (95% CI): 0.50 (0.43 to 0.58); n: 12 | −0.09 (−0.28 to 0.09) | 0.32 | |
| SEI, nurse assessment (observations) | mean (95% CI): 0.45 (0.26 to 0.64); n: 12 | mean (95% CI): 0.51 (0.35 to 0.68); n: 12 | −0.06 (CI −0.29 to 0.17) | 0.58 | |
| Duration of sleep, nurse assessment (observations) | median (range): 240 minutes (75 to 331.3); n: 14 | median (range): 243.4 minutes (0 to 344.1); n: 18 | not reported | 0.98 | |
| Duration of sleep, nurse assessment (observations) | 9 p.m. to midnight, mean (SD): 1.5 (± 1.6) hours; n: 41 midnight to 7 a.m., mean (SD): 4.5 (± 1.9) hours; n: 41 | 9 p.m. to midnight, mean (SD): 1.4 (± 1.3) hours; n: 41 midnight to 7 a.m., mean (SD): 4.3 (± 1.8) hours; n: 41 | not reported | 0.92 0.83 | |
| Outcome: quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| SEI (BIS) | Mean (95% CI): 0.39 (0.27 to 0.51); n: 12 | Mean (95% CI): 0.26 (0.17 to 0.36); n: 12 | 0.12 (CI −0.02 to 0.27) | 0.09 | |
| SEI (actigraphy) | Mean (95% CI): 0.73 (0.53 to 0.93); n: 12 | Mean (95% CI): 0.75 (0.67 to 0.83); n: 12 | −0.02 (CI −0.24 to 0.20) | 0.84 | |
| Quantity of nocturnal sleep (BIS) | Mean: 3.5 hours; n: 12 | Mean: 2.5 hours; n: 12 | Not reported | ‐ | |
| Outcome: anxiety or depression, or both | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| Anxiety (using VNR) | Participants with score ≥ 3: 12; n: 41 | Participants with score ≥ 3: 14; n: 41 | Not reported | 0.10 | |
| Outcome: mortality at 30 days | |||||
| Study | Measurement | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| Mortality in hospital | 14; n: 41 | 15; n: 41 | Not reported | 0.82 | |
| Outcome: length of stay in the ICU | |||||
| Study | Measurement | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| ´Number of days | Median (IQR): 14 (8 to 20); n: 41 | median (IQR): 12 (9 to 29); n: 41 | Not reported | 0.75 | |
* as reported by study authors
BIS: bispectral index
CI: confidence interval
EEG: electroencephalogram
IQR: interquartile range
n: number of randomized participants
PSG: polysomnography
RCSQ: Richards‐CampbellSleep Questionnaire
SD: standard deviation
SEI: sleep efficiency index
TST: total sleep time
VNR: verbal numeric range
Bourne 2008 reported a sleep efficiency index (SEI), which was defined as the ratio of a participant's total sleep time over the time available for night‐time sleep (9 hours, from 10 p.m. to 7 a.m.). Participants used the Richards‐Campbell Sleep Questionnaire (RCSQ) to report amount of sleep (Richards 2000), and study authors reported no difference in SEI using the RCSQ between groups according to participant sleep assessment (mean difference (MD) −0.09, 95% CI −0.28 to 0.09; P = 0.32; as reported by study authors). Similarly, study authors reported no difference in SEI between groups assessed with observation from nurses (MD −0.06, 95% CI −0.29 to 0.17; P = 0.58; as reported by study authors). We have reported mean SEI scores for each group as reported by study authors in Table 1.
Ibrahim 2006 reported duration of nocturnal sleep assessed with observation from nurses. Study authors reported similar median observed minutes of sleep between groups (P = 0.98).
Mistraletti 2015 reported duration of sleep observed during nursing shifts (from 9 p.m. to midnight, and midnight to 7 a.m.) with no difference between groups at each time point (P = 0.92, and P = 0.83, respectively).
We used the GRADE approach to downgrade the evidence to very low quality. We identified few studies with few participants. We noted differences in the dose of melatonin between studies (one study gave a dose a 10 mg, one study gave a dose of 3 mg, and one study gave two separate doses of 3 mg), and study authors in two studies noted differences in baseline characteristics between groups (Bourne 2008; Mistraletti 2015). Reports were by participants and by nurse assessment, which may not be comparable. One study used an ICU sedation protocol which was not comparable to the other studies, or standard in ICU management, and may influence generalizability of this study data (Mistraletti 2015). See summary of findings Table for the main comparison.
Quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG
Two studies (37 participants) reported quantity and quality of sleep using objective tools. Assessments were not comparable and we could not combine data in meta‐analysis.
Bourne 2008 used bispectral index (BIS) and actigraphy, and reported no difference in SEI between groups (MD 0.12, 95% CI −0.02 to 0.27; P = 0.09; and MD −0.02, 95% CI −0.24 to 0.20; P = 0.84, as reported by study authors, respectively). We have reported mean SEI scores for each group as reported by study authors in Table 1.
Bourne and colleagues also reported quantity of nocturnal sleep collected with BIS: study authors noted that nocturnal sleep was one hour longer in the melatonin group and that this difference was not statistically significant (see Table 1). Study authors also reported area under the curve (AUC) for BIS, with a 7% decrease for those participants who had melatonin; study authors reported that a decrease in AUC represented "better sleep" (MD −54.23, 95% CI −104.47 to −3.98; P = 0.04).
Foreman 2015 (12 participants) collected data for total sleep time using polysomnography (PSG). Study authors reported a large loss of participant data, reporting only one participant in each group with scorable data for days one and three. Study authors do not report sleep data by group.
We used the GRADE approach to downgrade the evidence to very low quality. We identified few studies with few participants. We noted differences in dose of melatonin (one study gave a dose a 10 mg, and one study gave a dose of 3 mg), and study authors in one study noted differences in baseline characteristics between groups. We noted a high risk of performance bias and high attrition in one study, which prevented adequate reporting. We also noted that BIS may not be an appropriate measurement tool for sleep in the ICU, and data from BIS may be less reliable. See summary of findings Table for the main comparison.
Secondary outcomes
Anxiety or depression, or both, as measured with the use of validated tools, such as the Hospital Anxiety and Depression Scale (HADS) (Zigmond 1983)
One study reported anxiety as measured on a verbal numeric range (VNR) (Mistraletti 2015; 82 participants). Study authors reported number of participants who had anxiety (VNR ≥ 3). We noted no difference between groups in the number of participants who scored ≥ 3 on the VNR for anxiety (P = 0.10). See Table 1.
We used the GRADE approach to downgrade the evidence to very low quality. We identified only one study with few participants, and study authors noted differences between groups in pre‐treatment with opiates. We were not certain whether use of VNR was reliable or comparable to HADS as a tool to measure anxiety. We could not be certain that ICU sedation protocols in Mistraletti 2015 were generalizable to most ICUs. See summary of findings Table for the main comparison.
Mortality at 30 days
Two studies (94 participants) reported mortality (Foreman 2015; Mistraletti 2015).
Foreman 2015 reported that one‐third of participants died. We could not include this data in analysis because data were not reported by group. Study authors did not report end time point for mortality data collection and we could not be certain that it was within 30 days.
Mistraletti 2015 reported mortality in ICU, and mortality in hospital. We have reported data for mortality in hospital, although we could not be certain that it was within 30 days; study authors reported no difference between groups (P = 0.82). See Table 1.
We used the GRADE approach to downgrade the evidence to very low quality. We identified few studies with few participants, and we noted a high risk of performance bias and attrition in one study and differences between study groups in pre‐treatment use of opiates in another study. We could not be certain that ICU sedation protocols in Mistraletti 2015 were generalizable to most ICUs. See summary of findings Table for the main comparison.
Length of stay in the ICU
One study reported length of ICU stay (Mistraletti 2015; 82 randomized participants), and noted no difference between groups (P = 0.75). See Table 1.
We used the GRADE approach to downgrade the evidence to very low quality. We identified only one study with few participants, and study authors noted differences between groups in pre‐treatment use of opiates. We could not be certain that ICU sedation protocols in Mistraletti 2015 were generalizable to most ICUs. See summary of findings Table for the main comparison.
Adverse events (such as nausea, headache, or dizziness)
Two studies (107 participants) reported adverse events (Bourne 2008; Mistraletti 2015).
Bourne 2008 reported that one participant in the melatonin group had a headache which was treated effectively with acetaminophen; and Mistraletti 2015 reported that one participant in the placebo group had a cutaneous rash, and two participants (one participant in each group) had excessive sleepiness, and treatment was discontinued for these participants.
We used the GRADE approach to downgrade the evidence to very low quality. We identified few studies with few participants. We noted differences in the dose of melatonin between studies and study authors noted differences between groups in baseline characteristics which could influence results. We could not be certain that ICU sedation protocols in Mistraletti 2015 were generalizable to most ICUs. See summary of findings Table for the main comparison.
Subgroup analysis
We did not have sufficient studies to combine data in meta‐analysis and we did not perform subgroup analysis. We described studies according to subgroups below.
1. Severity of the health condition based on APACHE II scores (or comparable severity measures): APACHE II scores less than 25; 25 to 35; greater than 35.
Three studies reported APACHE II scores, and all mean scores were less than 25 (Bourne 2008; Foreman 2015; Ibrahim 2006). One study reported SAPS II, with a mean score (SD) of 45.7 (± 18.2) in the melatonin group and mean (SD) score of 44.1 (± 15.3) in the control (Mistraletti 2015).
2. Mechanically ventilated participants versus those not mechanically ventilated
Two studies included participants that were mechanically ventilated (Bourne 2008; Mistraletti 2015): one study included both participants that were mechanically ventilated and not mechanically ventilated (Foreman 2015); and one study included participants who were weaning from mechanical ventilation.
3. Participants 65 years of age or older versus participants younger than 65 years
No studies reported inclusion of participants who were 65 years of age or older.
4. Participants in a surgical ICU versus those in a medical ICU
One study setting was described as a neurosurgical ICU (Foreman 2015); and one study setting was described as a surgical and medical ICU (Mistraletti 2015).
Sensitivity analysis
We did not perform sensitivity analysis because we did not combine data in meta‐analysis.
Comparison 2: melatonin versus another agent administered specifically to promote sleep
No studies compared melatonin with another agent.
Discussion
Summary of main results
We identified four randomized controlled trials with 151 participants. All studies compared melatonin to no agent; three studies used a placebo control; and one study compared melatonin with usual care.
Three studies assessed quantity and quality of sleep as measured through reports of participants, family members, or personnel assessments. Of these, one study reported measurements in terms of sleep efficiency index (SEI) and reported no difference between groups in SEI scores for participant assessment and for nurse assessment. Two studies reported no difference in observed sleep by nurse assessment.
Two studies assessed quantity and quality of sleep as measured by polysomnography (PSG), actigraphy, bispectral index (BIS), or electroencephalogram (EEG). Of these, one study used actigraphy and BIS and reported no difference between groups in SEI scores. This study also reported longer sleep in participants given melatonin, which was not statistically significant; and evidence of improved sleep in participants given melatonin through analysis of area under the curve of BIS data.
One study reported no difference between groups in anxiety, one study reported mortality with no difference between groups, and one study reported no difference between groups in length of ICU stay. Two studies reported data for adverse events: one study reported a headache in one participant given melatonin; and one study reported two participants with excessive sleepiness (one participant from each group) and one participant in the placebo group with a cutaneous rash.
Overall completeness and applicability of evidence
Included studies recruited critically ill participants in the intensive care unit and administered melatonin at night‐time with the intention of promoting sleep. Baseline data suggested that participants were similar in terms of illness severity measured with APACHE II or SAPS II. However, differences in detail in study reports prevented some appropriate comparisons between study participants; for example, we were unable to report primary diagnoses, mechanical ventilation status, and length of stay in the ICU prior to start of trial, for all study participants. Whilst all patients in the ICU may be subject to sleep disturbance, other factors (such as being mechanically ventilated) may exacerbate sleep disturbance and may influence the effect of melatonin.
We noted a difference in one study, in which the ICU used a sedation protocol that differed from standard ICU sedation management. Also, we noted differences in study designs with administered dose of melatonin varying between studies from 3 mg to 10 mg. Potential differences in study populations and heterogeneity in study design compromise the generalizability and applicability of these results to the general ICU population.
Quality of the evidence
All studies reported adequate methods of randomization, and three placebo‐controlled trials had blinded participants and personnel, and had low risks of performance and detection bias. One study had compared melatonin with usual care and we judged this study to have a high risk of performance and detection bias; we also noted high attrition in this study.
We included few studies with few participants in this review. We believe that sparse data reduced precision in the effect for each of our outcomes. Differences in dose of melatonin between studies introduced inconsistency at the study design level, and difference in sedation protocols in one study introduced indirectness to the outcome data. We could not be certain whether some differences between groups at baseline level in two studies had affected results. We identified insufficient studies to allow for subgroup analysis and were unable to explore whether differences in study populations could affect response to melatonin. Similarly, because of insufficient studies, we were unable to assess the risk of publication bias in this review through generation and interpretation of a funnel plot.
We identified only two studies that used objective measurement tools to measure sleep. One of these studies used PSG, which is designed specifically to measure sleep; however, this small study reported technical difficulties and a subsequent large loss of participant data. Another study used BIS monitoring, which is typically used to measure depth of anaesthesia; it is unclear whether this is an appropriate measurement tool for sleep in the ICU.
We used the GRADE approach to downgrade the evidence for each outcome to very low quality.
Potential biases in the review process
We conducted this review using Cochrane methodology, using two authors to select studies, extract data and assess risk of bias according to our published protocol (Lewis 2016b). We conducted a thorough search that included clinical trial registers, forward and backward citation tracking, and grey literature. Also, we contacted study authors to request additional study information or information regarding potential unpublished trials.
Agreements and disagreements with other studies or reviews
A review that looked at the effect of melatonin and melatonin receptor agonists on sleep and delirium in the ICU concluded that the role of pharmacological agents to promote sleep for prevention of delirium remained uncertain (Mo 2016); review authors suggest that additional clinical trials are necessary. Cochrane Reviews that have looked at melatonin in other settings have reported increased length of sleep with melatonin after disruption from shift work (Liira 2014), reduction in preoperative anxiety (Hansen 2015), and reduction in, or prevention of, jet lag (Herxheimer 2002). However, these participant groups are not comparable to critically ill patients in the ICU.
Study flow diagram
Risk of bias graph: review authors' judgements about each risk of bias item presented as percentages across all included studies.
Risk of bias summary: review authors' judgements about each risk of bias item for each included study. Blank spaces in figure indicate that outcomes were not reported by study authors, and therefore risk of bias was not completed for these domains.
| Melatonin compared with no agent for the promotion of sleep in adult patients in the ICU | ||||
| Patient or population: adult patients in the ICU Settings: ICUs, in Australia, Italy, UK, and US Intervention: melatonin Comparison: no agent | ||||
| Outcomes | Impacts | No of participants | Quality of the evidence | Comments |
| Quantity and quality of sleep as measured through reports of participants or of family members or by personnel assessments Data collected at end of follow‐up | In 1 study, participants completed the RCSQ and study authors reported no difference in SEI scores between groups. This was consistent with nurse assessment for which study authors also reported no difference in SEI scores between groups 2 studies reported no difference in duration of sleep observed by nurses | 139 (3 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies used different methods to report data |
| Quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG Data collected at end of follow‐up | In 1 study, investigators used BIS and actigraphy to record sleep. Study authors reported no difference in SEI scores with both tools. Study authors also reported longer sleep in participants given melatonin which was not statistically significantly different, and also reported evidence of improved sleep in participants given melatonin from analysis of AUC using BIS data 1 study used PSG, with a large loss of participant data at follow‐up, which prevented analysis of sleep data | 37 (2 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies differed in types of measurement tools |
| Anxiety or depression, or both Data collected at end of follow‐up | 1 study (using VNR ≥ 3) reported no evidence of a difference in anxiety scores between groups | 82 (1 study) | ⊕⊝⊝⊝ | We identified only one study and could not conduct meta‐analysis |
| Mortality Study authors did not report final timepoint for data collection. | 1 study reported one‐third of participants had died; number of deaths per group was not reported 1 study reported no evidence of a difference between groups in hospital mortality | 94 (2 studies) | ⊕⊝⊝⊝ | We did not conduct meta‐analysis because studies different in methods of reporting data |
| Length of stay in the ICU | One study reported no evidence of a difference in length of ICU stay between groups | 82 (1 study) | ⊕⊝⊝⊝ | We identified only 1 study and could not conduct meta‐analysis |
| Adverse events (such as nausea, dizziness and headache) Data collected at end of follow‐up | 1 study reported headache in one participant who was given melatonin 1 study reported a cutaneous rash in one participant in the control group, and 2 participants (1 participant in both groups) with excessive sleepiness | 107 (2 studies) | ⊕⊝⊝⊝ | We could not conduct meta‐analysis because studies different in reported types of adverse events |
| Acronyms and abbreviations AUC: area under the curve; BIS: bispectral index; EEG: electroencephalogram; ICU: intensive care unit; PSG: polysomnography; RCSQ: Richards‐Campbell Sleep Questionnaire; SEI: sleep efficiency index; VNR: verbal numeric range | ||||
| GRADE Working Group Grades of Evidence | ||||
| aWe downgraded by 2 levels for imprecision; there were few studies with few participants, and outcome measures included both personnel and participant reports. We downgraded by 1 level for study limitations; we noted differences in baseline characteristics in two studies which may have influenced results. We downgraded by 1 level for inconsistency; we noted differences in doses of melatonin given in each study. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in one study were generalizable to most ICUs bWe downgraded by 2 levels for imprecision; there were few studies very few participants, and outcome measures used different assessment tools which may not effectively measure sleep in the ICU patient. We downgraded by 1 level for study limitations; we noted differences in baselines characteristics in one study which may have influenced results. We downgraded 1 level for inconsistency; we noted differences in doses of melatonin given in each study. We downgraded by 1 level for study limitations; we noted high risk of performance bias and high attrition which prevented adequate outcome reporting cWe downgraded by 2 levels for imprecision; data was from one study with few participants, and we could not be certain whether this outcome was measured with an appropriate tool for patients in the ICU. We downgraded by 1 level for study limitations; pre‐treatment use of opiates differed between study groups. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs dWe downgraded by 2 levels for imprecision; there were few studies with few participants. We downgraded by 1 level for study limitations; we noted a high risk of performance bias and attrition bias in one study and we noted differences between groups in pre‐treatment use of opiates. We downgraded 1 level for inconsistency; doses of melatonin varied between studies. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs eWe downgraded by 2 levels for imprecision; data was from one study. We downgraded by 1 level for study limitations; pre‐treatment use of opiates differed between study groups. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs fWe downgraded by 2 levels for imprecision; there were few studies with few participants. We downgraded by 1 level for study limitations; we noted differences in baseline characteristics in two studies which may have influenced results. We downgraded by 1 level for indirectness; we could not be certain that ICU sedation protocols in 1 study were generalizable to most ICUs | ||||
| Outcome: quantity and quality of sleep as measured through reports of participants or family members or by personnel assessments | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| SEI, patient assessment (RCSQ) | mean (95% CI): 0.41 (0.24 to 0.59); n: 12 | mean (95% CI): 0.50 (0.43 to 0.58); n: 12 | −0.09 (−0.28 to 0.09) | 0.32 | |
| SEI, nurse assessment (observations) | mean (95% CI): 0.45 (0.26 to 0.64); n: 12 | mean (95% CI): 0.51 (0.35 to 0.68); n: 12 | −0.06 (CI −0.29 to 0.17) | 0.58 | |
| Duration of sleep, nurse assessment (observations) | median (range): 240 minutes (75 to 331.3); n: 14 | median (range): 243.4 minutes (0 to 344.1); n: 18 | not reported | 0.98 | |
| Duration of sleep, nurse assessment (observations) | 9 p.m. to midnight, mean (SD): 1.5 (± 1.6) hours; n: 41 midnight to 7 a.m., mean (SD): 4.5 (± 1.9) hours; n: 41 | 9 p.m. to midnight, mean (SD): 1.4 (± 1.3) hours; n: 41 midnight to 7 a.m., mean (SD): 4.3 (± 1.8) hours; n: 41 | not reported | 0.92 0.83 | |
| Outcome: quantity and quality of sleep as measured by PSG, actigraphy, BIS, or EEG | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| SEI (BIS) | Mean (95% CI): 0.39 (0.27 to 0.51); n: 12 | Mean (95% CI): 0.26 (0.17 to 0.36); n: 12 | 0.12 (CI −0.02 to 0.27) | 0.09 | |
| SEI (actigraphy) | Mean (95% CI): 0.73 (0.53 to 0.93); n: 12 | Mean (95% CI): 0.75 (0.67 to 0.83); n: 12 | −0.02 (CI −0.24 to 0.20) | 0.84 | |
| Quantity of nocturnal sleep (BIS) | Mean: 3.5 hours; n: 12 | Mean: 2.5 hours; n: 12 | Not reported | ‐ | |
| Outcome: anxiety or depression, or both | |||||
| Study | Measurement (tool) | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| Anxiety (using VNR) | Participants with score ≥ 3: 12; n: 41 | Participants with score ≥ 3: 14; n: 41 | Not reported | 0.10 | |
| Outcome: mortality at 30 days | |||||
| Study | Measurement | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| Mortality in hospital | 14; n: 41 | 15; n: 41 | Not reported | 0.82 | |
| Outcome: length of stay in the ICU | |||||
| Study | Measurement | Data* Intervention | Data* Control | Mean difference (95% CI)* | P value* |
| ´Number of days | Median (IQR): 14 (8 to 20); n: 41 | median (IQR): 12 (9 to 29); n: 41 | Not reported | 0.75 | |
| * as reported by study authors BIS: bispectral index | |||||
