Melatonin for blood pressure control in adults

Objectives

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

Critical objective

To assess the effects of oral melatonin supplementation (immediate‑release (IR) and controlled‑/sustained‑release CR/SR; any dose; ≥ 1 week) versus placebo or no treatment on change in systolic and diastolic blood pressure (SBP, DBP) in adults.

Important objectives

1. To examine dose‑response relationships between melatonin dose and changes in SBP and DBP.

2. To assess effects by key participant and intervention characteristics (prespecified subgroups): baseline blood pressure status; concomitant antihypertensive medication use; presence of diagnosed sleep disorder/insomnia; melatonin formulation (IR versus CR/SR); blood pressure measurement method (office versus ambulatory versus home; daytime versus nocturnal); age (< 65 versus ≥ 65 years); sex.

3. To evaluate adverse events (serious and non‑serious) and select patient‑important outcomes (quality of life, sleep quality).

4. To describe any reported longer‑term cardiovascular outcomes (e.g. incident cardiovascular disease events, mortality) when sufficient data are available. These analyses are exploratory given anticipated sparse data.

Background

Melatonin is a supplement that in recent years has grown in popularity and is primarily used to enhance sleep quality, an important factor in managing comorbidities such as hypertension and cardiovascular diseases [1, 2]. It varies in accessibility, available over‐the counter in many countries, such as the United States, whereas in other countries, including the United Kingdom and many European jurisdictions, it is a prescription‐only medicine [3].

This widespread use has prompted interest in its potential cardiovascular effects, a topic of significant clinical relevance given that blood pressure (BP) control remains suboptimal globally [4]. Poor adherence to prescribed antihypertensive therapy and inadequate control of hypertension are major challenges [5], resulting in the need for well‐tolerated adjunct or alternative strategies for people with hypertension, particularly those with such comorbidities as diabetes, metabolic syndrome, and cardiovascular diseases [5]. However, systematic reviews and meta‐analyses evaluating the role of melatonin in managing hypertensive disorders remain scarce, leading to uncertainty amongst physicians regarding its appropriate use.

Melatonin is available in two primary oral formulations: immediate‐release (IR) and controlled‐ or sustained‐release (CR/SR) [6]. Controlled‐release formulations have been commercially available since approximately 2007, though their uptake and prescription rates vary by region [7]. Existing evidence on the effects of these formulations is mixed. One meta‐analysis found that CR melatonin significantly reduced systolic blood pressure (SBP) only [1], whilst another suggested that IR melatonin supplementation significantly reduced both SBP and diastolic blood pressure (DBP) [5], although it did not include a dose‐response analysis. Since these publications, new randomised controlled trials (RCTs) have emerged, necessitating an updated analysis to refine our understanding of melatonin's role in BP regulation.

The dosage‐response relationship between melatonin supplementation and its effect on BP remains a critical uncertainty [ 1]. Whilst multiple clinical trials have investigated melatonin's efficacy in BP reduction, results have been inconsistent. Some trials report no significant effect, whilst others demonstrate a notable reduction. Melatonin’s potential advantages over traditional antihypertensive medications, particularly its accessibility in some markets, have been highlighted [1]. Beyond BP, melatonin has been studied for its potential benefits in various conditions including atherosclerosis, weight management, high‐density lipoprotein levels, diabetes, and metabolic syndrome [5, 8,9,10].

Dose response is a crucial component for delineating hazards and maximising the efficacy of the treatment and clinical response [11]. Its study can help establish optimal dosage, assess drug tolerability, side effects, and safety, and determine both the initial therapeutic dose and the maximum effective dose. [12]. Clinicians need to understand the interrelation between dosage, drug concentration in the bloodstream, and physiological responses, as this is crucial for effective and safe use of melatonin [12].

Furthermore, the long‐term safety of exogenous melatonin, including potential effects on endogenous secretion and discontinuation, is not well established. This review will therefore extract and report any data on long‐term adverse events or withdrawal phenomena when available.

Description of the condition

Blood pressure is the force exerted by the blood against the walls of the blood vessels [13]. SBP is the maximum pressure exerted in the arteries when the ventricles of the heart contract, whilst DBP is the minimum pressure in the arteries when the ventricles are relaxed. The difference between SBP and DBP is pulse pressure (PP = SBP − DBP), which tends to be ~40 mmHg in younger, healthy adults but rises with age; elevated PP can indicate increased arterial stiffness [14]. Mean arterial pressure (MAP) is the average arterial pressure across the cardiac cycle [15]. These indices guide clinical assessment and treatment decisions [16]. SBP and DBP are used for diagnosing hypertension, whilst MAP can indicate cardiovascular disease [17, 18].

Definitions of hypertension vary across major international guidelines. The 2025 American Heart Association/American College of Cardiology guideline defines office hypertension beginning at BP ≥ 130/80 mmHg and retains the 2017 category scheme (stage 1: 130 to 139/80 to 89; stage 2: ≥ 140/90) [19]. The 2023 European Society of Hypertension guideline (endorsing International Society of Hypertension principles) retains ≥ 140/90 mmHg for office diagnosis (grade 1) and specifies lower diagnostic thresholds for out‐of‐office measurements (e.g. home ≥ 135/85 mmHg; 24‐hour ambulatory mean ≥ 130/80 mmHg; nighttime ≥ 120/70 mmHg) [20]. We will accept study authors' definitions, record the criteria used, and extract baseline BP values to enable stratified analyses.

The World Health Organization (WHO) estimates that 1.28 billion adults aged 30 to 79 years worldwide have hypertension [4]. In 2023, the WHO reported that nearly half of adults with hypertension are unaware of their condition, and less than half (42%) are diagnosed and treated [4].

The prevalence of hypertension varies across regions, income levels, and gender. In 2023, the WHO African Region had the highest prevalence (27%), whilst the WHO Region of the Americas had the lowest (18%) [4]. Studies indicate that the prevalence has decreased in high‐income countries, but has increased in low‐ and middle‐income countries [21][22]. Furthermore, in 2019, the age‐standardised prevalence of hypertension amongst adults aged 30 to 79 years was higher in men (37.6%) than in women (33.3%) [23].

Numerous studies have shown hypertension to be a major determinant of death and chronic illnesses, including atrial fibrillation, heart valve diseases, chronic kidney disease, dementia, heart failure, and stroke [24]. The WHO reports that raised BP is responsible for an estimated 7.6 million deaths per year worldwide [25]. Other estimates suggest that high BP contributes to approximately 10 million deaths annually [26].

Description of the intervention and how it might work

Melatonin is a hormone naturally produced by the pineal gland that is primarily secreted at night in response to the light‐dark cycle and is central to synchronising and regulating sleep‐wake cycles [27, 28]. It plays a key role in maintaining circadian rhythms and influences various physiological functions, including immune response and antioxidative defence [29]. Due to its antioxidant and cytoprotective features, melatonin can provide therapeutic benefits in sleep disorders, jet lag, and cancer protection [28], as well as in neurodegenerative diseases [30].

Melatonin can be sourced from synthetic, plant‐derived, and micro‐organism‐derived forms [31]. Whilst the oral form is the most common, other administration methods such as subcutaneous, transdermal, and intranasal have also been researched [32].

Although melatonin is traditionally known for its role in sleep regulation, it also exhibits properties that may influence both SBP and DBP. The compound's multifaceted influence on BP regulation is mediated through diverse biological mechanisms. These include interactions with melatonin 1 (MT1) and melatonin 2 (MT2) G‐protein coupled receptors, which significantly modulate vascular tone [33], and its antioxidant properties, particularly in scavenging reactive oxygen species and enhancing mitochondrial electron transport chain efficiency ​[34]. Other possible mechanisms of melatonin in BP regulation include reduction of myeloperoxidase activity, stimulation of tissue factor pathway inhibitor, sympathetic inhibition, and direct vasodilation [7].

Why it is important to do this review

Given the widespread use of melatonin, as either an over‐the‐counter or as a prescribed supplement, and its increasing popularity for potential BP benefits, it is crucial to comprehensively understand its effects on BP. This is particularly important for individuals taking antihypertensive medications, as well as those with comorbidities like diabetes, metabolic syndrome, renal disorders, and cardiovascular diseases, where potential interactions between melatonin and prescribed medications could be significant.

The existing literature on melatonin and BP is limited by several factors. Many studies have small sample sizes, short durations, and methodological limitations, preventing any definitive conclusions [35]. Additionally, there is a lack of standardised dosing regimens and limited exploration of the effects of melatonin in specific populations, such as individuals with comorbidities or those taking antihypertensive medications. Furthermore, the long‐term effects of melatonin supplementation on cardiovascular outcomes remain unclear.

This systematic review and dose‐response meta‐analysis aims to address these limitations by synthesising evidence from recent RCTs to provide a comprehensive and up‐to‐date assessment of melatonin's impact on BP. By analysing the dose‐response relationship, this review aims to identify optimal dosages and potential thresholds for BP reduction. Additionally, subgroup analyses will explore the effects of melatonin in specific populations, including those with comorbidities and varying demographic characteristics. The review will also evaluate the safety and tolerability of melatonin by examining the incidence of adverse events, contributing to a more comprehensive understanding of its risk‐benefit profile.

The findings of this review will have implications for clinical practice and public health. If melatonin proves to be an effective and safe adjunct therapy for BP management, it could offer a cost‐effective and accessible alternative or complement to traditional antihypertensive medications. This is particularly relevant in low‐ and middle‐income countries, and underinsured populations in high‐income countries, where access to health care and medications may be limited. Moreover, understanding the dose‐response relationship and subgroup effects will enable clinicians to personalise treatment plans, optimising the benefits of melatonin whilst minimising potential risks. By addressing the existing knowledge gaps and providing robust evidence, this review will contribute to evidence‐based decision‐making regarding the use of melatonin for BP regulation in adults.

Objectives

Critical objective

To assess the effects of oral melatonin supplementation (immediate‑release (IR) and controlled‑/sustained‑release CR/SR; any dose; ≥ 1 week) versus placebo or no treatment on change in systolic and diastolic blood pressure (SBP, DBP) in adults.

Important objectives

1. To examine dose‑response relationships between melatonin dose and changes in SBP and DBP.

2. To assess effects by key participant and intervention characteristics (prespecified subgroups): baseline blood pressure status; concomitant antihypertensive medication use; presence of diagnosed sleep disorder/insomnia; melatonin formulation (IR versus CR/SR); blood pressure measurement method (office versus ambulatory versus home; daytime versus nocturnal); age (< 65 versus ≥ 65 years); sex.

3. To evaluate adverse events (serious and non‑serious) and select patient‑important outcomes (quality of life, sleep quality).

4. To describe any reported longer‑term cardiovascular outcomes (e.g. incident cardiovascular disease events, mortality) when sufficient data are available. These analyses are exploratory given anticipated sparse data.

Methods

We will conduct this systematic review and meta‐analysis in accordance with the Methodological Expectations for Cochrane Intervention Reviews (MECIR) [36] and report it following the PRISMA 2020 guidelines [37].

Criteria for considering studies for this review

PICO criteria are as follows.

1. Population: adults (≥ 18 years) of any sex, ethnicity, or setting; includes normotensive or hypertensive participants with or without comorbid conditions (e.g. diabetes, cardiovascular disease, renal disorders, metabolic syndrome).

2. Intervention: oral melatonin supplementation (any formulation: IR and CR/SR) at any dosage for a treatment duration of ≥ 1 week.

3. Comparators: placebo or no treatment; trials comparing different melatonin doses/formulations are also eligible (data will be used in dose‑response analyses).

4. Outcomes: BP measures (SBP, DBP; MAP; PP; nocturnal dipping; others specified below); adverse events (serious adverse events (SAEs) and non‐serious AEs); quality of life; sleep quality; longer‑term cardiovascular outcomes when reported.

Types of studies

All RCTs including cross‐over, cluster‐RCTs, or factorial RCTs will be eligible irrespective of blinding. RCTs are considered the gold standard for assessing the efficacy and safety of interventions due to their rigorous design, which significantly minimises bias. We will exclude all other types of study designs (non‐RCTs and observational studies).

Including only RCTs in this meta‐analysis allows for a more homogeneous data set, reducing variability caused by different study designs and enhancing the precision of the aggregated effect estimates. Furthermore, focusing on RCTs provides a more trustworthy foundation for making evidence‐based decisions and recommendations, particularly important in clinical and public health contexts.

Types of participants

We will include adult participants (≥ 18 years) of any gender, ethnicity, and geographic location. Studies enrolling participants with hypertension, regardless of the presence or absence of additional pre‐existing conditions such as diabetes mellitus, metabolic syndrome, cardiovascular disease, or renal disorders, will be eligible. We will also include studies enrolling only healthy participants without pre‐existing conditions.

Types of interventions

The intervention of interest is oral melatonin supplementation, including both IR and CR/SR formulations. Eligible studies will include those that administered melatonin at any dose for ≥ 1 week. We will consider RCTs comparing melatonin to placebo or no treatment, as well as those comparing different doses or formulations of melatonin, for inclusion. We will exclude studies involving a single‐dose (one‐time) administration of melatonin.

Outcome measures

We will assess the impact of oral melatonin supplementation (IR and CR/SR) on BP‐related and patient‑important outcomes. These outcomes are categorised as 'critical' or 'important' based on their relevance to clinical decision‐making regarding melatonin's impact on BP. Unless otherwise specified, outcomes will be measured as the change from baseline at the end of the intervention period (end‐of‐treatment). We will extract data as the mean change from baseline to end‐of‐treatment.

Critical outcomes

The critical outcomes of this review are changes from baseline at the end of treatment in the following: SBP in mmHg, DBP in mmHg, and incidence of adverse events (SAEs; common non‑serious AEs such as headache, dizziness, nausea).

Important outcomes

Important outcomes include relevant physiological measures, patient‐reported outcomes, safety data, and longer‐term effects, as follows.

1. Change in MAP (mmHg)

2. Change in PP (mmHg)

3. Nocturnal BP dipping (assessed as percentage or absolute change from baseline to end‐of‐treatment)

4. Quality of life (QoL) (assessed using validated generic questionnaires (e.g. 36‐Item Short Form Health Survey (SF‐36), EQ‐5D), measured as mean change from baseline score at end‐of‐treatment)

5. Sleep quality (assessed using validated questionnaires (e.g. Pittsburgh Sleep Quality Index (PSQI), Epworth Sleepiness Scale (ESS)), measured as mean change from baseline score at end‐of‐treatment)

6. Heart rate (measured in beats per minute at end‐of‐treatment)

7. 24‑hour BP variability metrics

8. Long‐term outcomes: assessed as incidence of events or survival at follow‐up exceeding 13 weeks (> 13 weeks post‐intervention start):

   1. incident heart disease (e.g. heart failure, myocardial infarction, cerebrovascular disease);

   2. incident comorbid conditions (e.g. renal failure);

   3. all‐cause mortality/survival.

Timing of outcome assessment: we will assess outcomes (BP changes, adverse events, QoL, sleep) at the final time point reported during the intervention period (end‐of‐treatment). We will define follow‐up as short‐term (≤ 6 weeks), mid‐term (> 6 weeks to ≤ 13 weeks), and long‐term (> 13 weeks). Long‐term outcomes (incident CVD, etc.) will be extracted if reported at long‐term follow‐up (i.e. > 13 weeks post‐intervention start).

Search methods for identification of studies

Electronic searches

We will search the following databases from inception to 31 December 2025 or the date of completion of electronic search (whichever is latest), with no language restrictions:

1. Cochrane Central Register of Controlled Trials (CENTRAL, the Cochrane Library) (1996 to current issue);

2. MEDLINE (Ovid) (1946 to present);

3. Embase (Ovid) (1974 to present) (with Embase Classic 1947 to 1973);

4. Web of Science Core Collection (Clarivate) including:

   1. Science Citation Index Expanded (1900 to present);

   2. Social Sciences Citation Index (1956 to present);

   3. Arts & Humanities Citation Index (1975 to present);

   4. Emerging Sources Citation Index (2005 to present);

5. Scopus (Elsevier) (1960 to present).

Before data synthesis, we will re‐run the searches to capture any newly indexed or ahead‐of‐print records.

A draft MEDLINE (Ovid) strategy is provided in Supplementary material 1 and will be translated for the other databases using appropriate controlled vocabulary and syntax. The Cochrane Highly Sensitive Search Strategy for randomised trials has been incorporated.

Searching other resources

We will actively check for post‐publication amendments (retractions, expressions of concern, corrigenda, errata) for all studies progressing to full‐text review stage and for all included studies prior to final analysis. This will involve checking the citation record in databases like PubMed, checking the publisher's website for notices linked to the article, and cross‐referencing included studies with the Retraction Watch Database. The implications of any identified amendments will be assessed and documented.

Data collection and analysis

We will analyse data using RevMan [38] for standard pair‐wise meta‑analyses, and R (version 4.5.0 or later) [39] for additional analyses, including meta‑regression (metafor package) and dose‑response meta‑analysis (dosresmeta package).

Selection of studies

Two review authors will independently screen the titles and abstracts of identified studies against the eligibility criteria. We will retrieve the full‐text reports of potentially eligible studies, and the same two review authors will independently assess the full texts for inclusion in the review. Any disagreements will be resolved through discussion or in consultation with a third review author. We will document and report the reasons for the exclusion of full‐text studies in a PRISMA flow diagram.

Data extraction and management

Two review authors will independently conduct data extraction using a standardised data extraction form developed in Covidence software [40]. We will extract the following information: study characteristics (e.g. design, setting, country), participant characteristics (e.g. age, sex, comorbidities, baseline BP), intervention details (e.g. dose, duration, formulation), and outcome data at all reported time points. For studies with missing or unclear data, we will attempt to contact the study authors for clarification. If data are reported in graphical format, we will use digital tools to extract numerical values. Any disagreements between review authors will be resolved through discussion; if consensus cannot be reached, a third review author will be consulted.

Risk of bias assessment in included studies

Two review authors will independently assess risk of bias in included RCTs using the Cochrane RoB 2 tool [41], which will be complemented by the ROB‐ME tool [42]. Any disagreements will be resolved through discussion or in consultation with a third review author. The risk of bias assessment will inform the GRADE assessment of the certainty of evidence.

In line with the Cochrane RoB 2 tool, the effect of interest in this review is defined as the effect of assignment to the intervention at baseline, irrespective of adherence to the intervention protocol. Accordingly, the RoB 2 tool will be applied to assess risk of bias for the intention‐to‐treat effect. This approach is consistent with the review's objective to assess the effectiveness of oral melatonin supplementation under real‐world conditions.

We will assess risk of bias using the RoB 2 tool for all critical and important outcomes that contribute to the summary of findings table (see Certainty of the evidence assessment). We will also assess risk of bias for long‐term cardiovascular outcomes where applicable.

The RoB 2 tool evaluates bias across the following five domains.

1. Bias arising from the randomisation process

2. Bias due to deviations from the intended interventions

3. Bias due to missing outcome data

4. Bias in measurement of the outcome

5. Bias in selection of the reported result

For each domain and for the overall risk of bias, we will assign one of the following judgements: low risk of bias, some concerns, or high risk of bias. These judgements will be based on responses to the signalling questions within each domain, using the tool's decision algorithms. We will determine the overall risk of bias for each outcome as follows:

1. low risk of bias: all domains are judged to be at low risk of bias;

2. some concerns: at least one domain raises some concerns, and none are at high risk of bias;

3. high risk of bias: one or more domains are rated as at high risk of bias, or if multiple domains raise some concerns.

Measures of treatment effect

For continuous outcomes measured on the same scale (e.g. SBP, DBP, MAP, PP in mmHg), we will calculate mean differences (MDs) with 95% confidence intervals (CIs). In a randomised trial, analyses based on change‐from‐baseline scores and those based on post‐intervention scores are expected to address the same underlying intervention effect. Therefore, where studies report a mix of these outcomes, we will combine them in the meta‐analysis using the MD method, ensuring the appropriate means and standard deviations (SDs) are used for each study.

For continuous outcomes measured using different instruments but representing the same underlying construct (e.g. QoL, sleep quality), we will calculate standardised mean differences (SMDs) with 95% CIs. This method standardises the results of the studies to a uniform scale before they can be combined.

For dichotomous outcomes (e.g. proportion experiencing ≥ 1 adverse event; SAEs), we will calculate risk ratios (RRs) with 95% CIs. If events are rare and effect sizes small, we may apply the Peto odds ratio method when its assumptions are met.

For dose‑response analyses, we will model change in BP (mmHg) per mg/day of melatonin (linear component) and, where data allow, estimate changes across the observed dose range from non‑linear spline models.

Unit of analysis issues

We will analyse data according to the unit of randomisation. For parallel‑group RCTs, we will use study‑reported summary results with the individual as the unit of randomisation.

1. Cluster‑randomised trials. When trial authors report effect estimates that appropriately account for clustering, we will use those directly. If clustering was ignored, we will adjust using the 'effective sample size' (or variance inflation) method with an intracluster correlation coefficient (ICC) from the trial report or, if unavailable, from external sources judged to be clinically similar. We will enter adjusted effect estimates using the generic inverse‑variance method.

2. Cross‐over trials. We will extract paired analyses (or data permitting derivation of paired estimates) that account for within‑participant correlation. If paired data are unavailable, we will use first‑period data in sensitivity analyses when carry‑over is a concern.

3. Multi‑arm trials (including factorial designs). To avoid double‑counting, we will either (i) combine relevant intervention arms, or (ii) split shared comparator groups. We will document how each multi‑arm study was handled.

4. Multiple time points. End‑of‑treatment is the primary analytic time point; we will extract additional prespecified follow‑up categories (short‑term, mid‑term, long‑term) for descriptive and sensitivity purposes.

5. Dose‑response meta‑analysis (DRMA). Several eligible trials include multiple melatonin dose arms. For DRMA, we will extract arm‑level summary data (mean change in BP and its variance) for each melatonin dose and its comparator. We will estimate study‑specific dose‑response slopes (linear and, when ≥ 2 non‑zero dose levels are available, non‑linear) using generalised least squares methods for summarised dose‑response data [43, 44]. This approach reconstructs the within‑study covariance amongst dose categories so that correlated estimates are correctly weighted. The resulting study‑level coefficients will then be pooled in a multivariate random‑effects meta‑analysis (see Synthesis methods for full details). We will not conduct individual participant data analyses.

Dealing with missing data

We will attempt to obtain missing or unclear summary data (e.g. group means, SDs, numbers of events) by contacting study authors or sponsors (up to two attempts). We will use available‑case, study‑reported data in our primary analyses.

When dispersion statistics are missing, we will derive SDs from reported standard errors (SEs), CIs, P values, or other statistics where possible. If derivation is impossible, we will borrow an SD from clinically and methodologically similar studies in the meta‑analysis (e.g. pooled or median SD); we will clearly flag these imputations and test their influence in sensitivity analyses.

For each study and outcome, we will record the proportion of randomised participants with missing outcome data in each arm. If ≥ 20% of participants are missing overall, or the absolute difference between arms is ≥ 10 percentage points, we will assess robustness in sensitivity analyses by:

1. excluding these studies; and

2. applying prespecified, arm‑level informative‑missingness assumptions:

   1. same‐as‐observed: missing participants are assumed to have the same mean/risk as observed participants in their own arm;

   2. conservative against the intervention: missing participants in the intervention arm are assigned a worse outcome (e.g. higher event risk or a negative δ shift for continuous outcomes), whilst missing in the control arm are assigned the observed arm mean/risk;

   3. relative‐risk (or δ) multiplier: for dichotomous outcomes, assume the risk amongst missing participants is k times the observed risk in that arm (k = 1.2 and 1.5); for continuous outcomes, apply ± 0.2 SD and ± 0.5 SD shifts.

The extent and handling of missing outcome data will inform RoB 2 judgements, ROB‑ME assessments of risk of bias due to missing evidence [42], and GRADE certainty of evidence ratings. Studies will not be excluded from the review solely for having unusable data; if summary data cannot be obtained or derived, the study will be described narratively.

Reporting bias assessment

We will assess the potential for publication bias when at least 10 studies are available for a given meta‑analysis, using funnel plot asymmetry (visual) and, where appropriate, statistical tests such as Egger’s regression. With fewer studies, interpretation is unreliable, and we will describe this limitation narratively.

Synthesis methods

We will extract all included studies into RevMan [38]. Pair‐wise random‑effects meta‑analyses of any oral melatonin versus placebo/no treatment will form the evidence base for GRADE certainty of evidence ratings and summary of findings conclusions. Dose‑response analyses are exploratory and hypothesis‑generating.

We prespecify random‑effects meta‑analysis for primary quantitative syntheses because we anticipate substantial clinical and methodological diversity (e.g. melatonin dose, formulation, treatment duration, participant characteristics, baseline BP). Model choice will not be based on observed I² values.

When two or more studies report the same BP measurement method (e.g. office SBP/DBP; 24‑hour ambulatory SBP/DBP; home BP), we will conduct separate random‑effects meta‑analyses by method. If individual studies report multiple methods, we will preferentially extract ambulatory 24‑hour data (most comprehensive), but will include alternative methods in method‑specific analyses; selection rules will be documented a priori in the data extraction form.

Pre‑pooling conceptual appraisal of heterogeneity. Before conducting any quantitative synthesis, two review authors will independently consider whether studies are sufficiently similar in key PICO elements to justify pooling.

1. Population case‑mix (e.g. normotensive versus hypertensive; concomitant antihypertensive therapy; presence of sleep disorders)

2. Intervention characteristics (melatonin formulation, dose metric, treatment duration)

3. Comparator type (placebo versus no treatment; similar background care)

4. Outcome definition and measurement timing (office versus ambulatory versus home BP; end‑of‑treatment versus other time points)

5. Overall risk of bias and major study design differences (parallel versus cross‐over versus cluster)

Any disagreements will be resolved by discussion; if important, irreconcilable conceptual differences remain, we will not pool and will instead apply the structured narrative approach described below.

We will quantify heterogeneity using the I² statistic and Cochran’s Q (P < 0.10 suggesting statistical heterogeneity), but interpretation will also consider the above clinical and methodological diversity, visual inspection of forest plots, and overlap of CIs.

Dose‑response meta‑analysis (DRMA)

To investigate the relationship between melatonin dose and BP changes, we will conduct a two‑stage DRMA using the 'dosresmeta' package [44] in R. In stage 1, study‑specific dose‑response trends will be estimated via generalised least squares (GLS), which reconstructs or approximates the within‑study variance‑covariance matrix amongst dose categories [43, 45] (implemented in dosresmeta). In stage 2, these study‑specific trend coefficients will be pooled using multivariate random‑effects meta‑analysis to account for between‑study heterogeneity [45].

We will fit both linear and non‑linear models. Non‑linear relationships will be modelled using restricted cubic splines (RCS). When data are adequate (≥ 3 non‑zero dose levels across ≥ 3 studies), knots will be placed at the 5th, 35th, 65th, and 95th percentiles of the observed dose distribution – a commonly used percentile spread that provides stable performance in sparse summarised‑data settings whilst allowing flexibility in the tails [46]. If data are very sparse (e.g. only one non‑zero dose per study or fewer than three studies with multiple categories), we will reduce the number of knots (e.g. 3‑knot specification at ~10th, 50th, 90th percentiles) or revert to a linear trend only; all departures from the primary knot plan will be documented. Model selection will be guided by goodness‑of‑fit statistics (Akaike information criterion/Bayesian information criterion (AIC/BIC)) and a Wald (or likelihood ratio) test for non‑linearity (P < 0.10 threshold for spline terms beyond the linear component).

Dose coding rules. Doses reported as ranges will be assigned their midpoint. For open‑ended upper ranges (e.g. "≥ 10 mg"), the width will be assumed to be equivalent to the adjacent lower interval; sensitivity analyses will vary this assumption (e.g. +25%, +50%). All doses will be standardised to mg/day. The reference dose (placebo/no treatment) will be assigned zero [43]. Studies using active comparators without a zero‑dose reference will be excluded from the primary DRMA; where feasible, we will explore transformations (e.g. re‑anchoring to the lowest melatonin dose) in sensitivity analyses and narratively report if transformations are not defensible.

Estimation details. Within‑study covariances amongst multiple melatonin dose groups will be approximated using the Greenland & Longnecker method (default covariance = "gl" in dosresmeta). If required (e.g. incomplete cell counts), we will consider alternative approximations (Hamling re‑construction) and compare results in sensitivity analyses. Between‑study variance‑covariance components will be estimated by restricted maximum likelihood (REML; default); if models fail to converge or data are extremely sparse, we will fit simplified structures (e.g. diagonal ψ) or fixed‑effect models as sensitivity checks.

Assumptions. We will estimate study‑specific dose‐response trends under the following standard summarised‑data assumptions.

1. Arm‑level effect estimates (e.g. mean change in SBP) are approximately normally distributed and unbiased for their true arm means.

2. Reported (or derived) variances correctly reflect within‑arm sampling error.

3. For multi‑arm parallel trials, correlations amongst ≥ 2 non‑zero melatonin dose arms arise solely because each is compared with a common reference (usually placebo/no melatonin); we reconstruct the resulting within‑study variance‐covariance matrix using the Greenland & Longnecker generalised least squares approach.

4. Assigned melatonin dose (mg/day) adequately represents actual exposure; ranges are coded at their midpoint (open upper ranges imputed as width of adjacent lower range; varied in sensitivity analyses).

5. Relationships are assumed linear within small dose intervals; flexible restricted‑cubic‑spline models relax global linearity when data permit; we do not extrapolate beyond the highest observed dose.

6. Differences in release formulation (IR versus CR/SR) and treatment duration may introduce additional between‑study heterogeneity; these factors are handled in subgroup/meta‑regression/stage‑2 models rather than in the within‑study covariance construction.

Data sufficiency. We will attempt DRMA when ≥ 2 melatonin dose levels (including zero) are available in ≥ 2 studies; non‑linear spline models require ≥ 3 non‑zero dose levels across ≥ 3 studies. When required input data (arm n, mean change, SD/SE) are incomplete, we will attempt reconstruction (Hamling‑style re‑calculation, author contact); otherwise the study will contribute to pair‐wise meta‑analysis only.

Sensitivity checks. We will (a) compare GLS‑based models with models assuming independence (diagonal covariance) when data are sparse; (b) vary dose coding assumptions (+25%, +50% width for open ranges); and (c) compare linear versus spline fits. Material differences will be reported.

We will present results as pooled dose‑response curves with 95% confidence bands and numerically as the estimated BP change (mmHg) per 1 mg/day melatonin increment from the best‑fitting model. R code for all analyses will be made available in the Supplementary Materials to ensure reproducibility. If fewer than three studies report multiple doses – limiting feasibility of non‑linear modelling – we will report linear trends only and explicitly caution against extrapolation beyond observed data.

Narrative synthesis/SWiM fallback

If quantitative synthesis (meta‑analysis) is inappropriate for specific outcomes, for example because the pre‑pooling conceptual review (above) indicates that studies are not comparable; there is substantial unexplained statistical heterogeneity (e.g. I² > 75% after planned subgroup/meta‑regression exploration); or data are insufficient (fewer than two studies reporting the outcome), we will conduct a narrative synthesis following the Synthesis Without Meta‑analysis (SWiM) reporting guideline [47]. This will involve the following.

1. Grouping studies based on key characteristics relevant to the review question (e.g. population type (normotensive versus hypertensive), intervention dose categories, duration of treatment, overall risk of bias).

2. Structured tabulation presenting key details for each study within these groups, including study characteristics, risk of bias judgements, and reported outcome data (effect estimates, CIs, direction of effect).

3. Utilising visual displays to complement the narrative, such as forest plots without the summary diamond (potentially ordering or grouping studies within the plot by key characteristics) or other relevant plots where appropriate.

4. Textual synthesis describing the characteristics and findings of included studies, focusing on patterns in the direction, magnitude, and consistency of effects within and across the prespecified groups, and explicitly considering study precision and risk of bias. We will avoid 'vote counting' based solely on statistical significance, and instead will comment on (a) the proportion of studies favouring melatonin versus comparator, (b) typical effect size ranges (reporting medians and ranges when comparable metrics are available), and (c) whether any observed differences appear to be clinically important (e.g. ~5 mmHg change in SBP is often considered meaningful, but we will defer to thresholds prespecified in individual trials where available and will not impose a hard cut‑off for synthesis).

5. Integration of methodological quality by signalling (in tables/figures and text) which contributing studies are at high versus low risk of bias; patterns driven primarily by high‑risk studies will be flagged as less credible.

6. Assessment of reporting limitations (selective outcome reporting, missing summary data) to inform ROB‑ME and GRADE certainty of evidence ratings.

7. Transparent reporting of the decision not to pool, including which pooling criteria were not met, and any attempts made to resolve heterogeneity.

8. Findings from the narrative synthesis will inform the summary of findings table and GRADE assessment; where only narrative evidence is available, certainty ratings will reflect indirectness, imprecision, and risk of bias accordingly.

Investigation of heterogeneity and subgroup analysis

We will investigate between‑study heterogeneity in three complementary steps: (1) a pre‑pooling conceptual appraisal of clinical and methodological comparability (see Synthesis methods); (2) statistical indices of residual heterogeneity; and (3) a priori subgroup and meta‑regression analyses when data permit.

1. Pre‑pooling conceptual appraisal

Before quantitative synthesis, two review authors will independently consider whether studies are sufficiently similar across key PICO features to justify pooling: participant case‑mix (e.g. baseline BP status; concomitant antihypertensive therapy; presence of sleep disorders), intervention characteristics (melatonin formulation, dose metric, treatment duration), comparator type (placebo versus no treatment; background care), outcome definition/measurement timing (office versus ambulatory versus home BP; daytime versus nocturnal; end‑of‑treatment versus other time points), and major design/risk of bias differences (parallel versus cross‐over versus cluster). Any disagreements will be resolved by discussion; if irreconcilable, we will not pool studies for that outcome, and will instead apply the structured narrative/SWiM approach.

2. Statistical assessment

For each meta‑analysis, we will examine:

• forest plot patterns (direction, magnitude, and CI overlap);

• I² (percentage of variability due to heterogeneity rather than sampling error);

• Tau² (between‑study variance estimate from the random‑effects model);

• Cochran’s Q test (P < 0.10 taken as indicative, not definitive, evidence of heterogeneity).

These indices will flag unexplained variability but will not, in isolation, determine model choice, pooling decisions, or subgroup interpretation. Interpretation will be contextualised using the conceptual appraisal described above.

3. Prespecified subgroups (categorical effect modifiers)

Where ≥ 2 studies contribute data per category (≥ 3 desirable), we will conduct subgroup analyses (random‑effects) for the following factors.

Factor	Categories/approach	Rationale
Melatonin formulation	IR vs CR/SR	Distinct pharmacokinetics; differential nocturnal coverage
Concomitant antihypertensive medication	Any vs none; exploratory by drug class if ≥ 3 studies per class	Potential additive/synergistic or ceiling effects
Diagnosed sleep disorder/insomnia	Yes vs no	Underlying circadian disruption may modify response.
Baseline BP category	Normotensive; elevated; hypertensive (per study definition)	Baseline risk/starting BP may influence absolute and relative effects.
BP measurement method	Office; 24‑hour ambulatory; home (explore daytime vs nocturnal ambulatory blood pressure monitoring)	Method‑specific variability; melatonin hypothesised to affect nocturnal BP
Age	< 65 vs ≥ 65 years	Age‑related vascular stiffness/autonomic changes
Sex	Male vs female	Possible sex‑specific pharmacodynamics/endogenous melatonin profiles

Subgroup analyses supported in RevMan [38] will use the test for subgroup differences. We will conduct additional exploratory subgrouping (e.g. antihypertensive drug class) in R [39].

Meta‑regression (continuous moderators)

When ≥ 10 studies provide the necessary data, we will conduct random‑effects meta‑regression in R (metafor) to examine whether treatment effect varies with:

1. mean baseline SBP (primary continuous moderator);

2. mean baseline DBP (secondary);

3. additional continuous covariates (e.g. mean age, % female) if data are sufficient and collinearity is manageable.

We will interpret regression coefficients as the change in treatment effect per unit increase in the moderator (e.g. mmHg greater reduction in SBP per 10‑millimetres of mercury higher baseline SBP). We will present fitted lines with 95% confidence bands where feasible.

Linkage with dose‑response meta‑analysis

We will explore effect modification (e.g. by formulation, baseline BP) within the two‑stage dose‑response framework – data permitting – by including study‑level moderators in stage‑2 multivariate models (interaction between dose slope and moderator). Given the anticipated sparsity, these analyses will be exploratory.

Interpretation of subgroup and meta‑regression findings

Interpretation will consider the following.

1. Direction and magnitude of subgroup‑specific effects (clinical relevance, not only statistical significance)

2. Overlap (or lack) of CIs between subgroups

3. Residual heterogeneity within subgroups (I²within, Tau²within) to assess explanatory value

4. Statistical evidence from tests for interaction (subgroup difference Qbetween; meta‑regression P value), recognising low power and multiplicity

5. Biological plausibility, prespecification, and consistency across related outcomes/time points

We will not base conclusions on the P value of the interaction test alone. Guidance from the Cochrane Handbook for Systematic Reviews of Interventions [48] and recent recommendations on credible subgroup effects will inform judgements about the credibility of any apparent effect modifiers.

Equity‐related assessment

We will assess the representation of different ethnicities, socioeconomic groups, and geographic regions in the included studies. We will explore whether the effects of melatonin on BP differ across these groups using subgroup analyses or meta‐regression. If data allow, we will also assess the potential impact of melatonin on health disparities related to BP.

Sensitivity analysis

Primary quantitative syntheses use random‑effects models. We will undertake the following prespecified sensitivity analyses to evaluate the robustness of our findings. Unless otherwise noted, analyses apply to both standard pair‑wise meta‑analyses and the two‑stage dose‑response models (DRMA), conditional on data sufficiency.

1. Model specification: re‑analyse using fixed‑effect models. For DRMA, fit fixed‑effect stage‑2 models (assuming common trend parameters) when feasible. Compare effect estimates and CIs.

2. Risk of bias: exclude studies rated at overall high risk of bias (RoB 2). If ≥ 10 studies remain, compare pooled effects.

3. Attrition/missing outcome data: exclude studies with ≥ 20% missing outcome data overall or ≥ 10 percentage‑point differential missingness between arms; compare with the primary analysis. For included studies above the threshold, apply the prespecified informative‑missingness scenarios described in Dealing with missing data.

4. Cluster‐randomised trials: exclude cluster‑randomised trials that required ICC imputation; alternatively, vary assumed ICCs across plausible ranges (e.g. 0.01 to 0.05) to assess the impact on pooled effects.

5. Cross‐over trials: (a) exclude cross‐over trials entirely; (b) restrict to first‑period data where carry‑over is likely or paired analyses unavailable; compare to primary results including appropriately analysed cross‐over data.

6. Imputed dispersion: re‑run analyses excluding studies with imputed SDs; and, separately, substitute low/high plausible SD values (e.g. ± 25% of pooled SD) to evaluate the influence on standardised effects.

7. Dose coding (DRMA only): vary assumptions for converting dose ranges to midpoints and for open‑ended upper categories (e.g. +25%, +50% wider than adjacent interval); assess impact on slope and curve shape.

8. Spline specification (DRMA only): compare primary 4‑knot restricted cubic spline to simplified 3‑knot model and to linear model; document convergence and fit (AIC/BIC).

9. Between‑study variance estimators: compare restricted maximum likelihood (REML) (primary) with alternative estimators (e.g. DerSimonian‑Laird, Paule‑Mandel) in standard meta‑analyses when ≥ 5 studies.

10. Influence diagnostics: conduct leave‑one‑out analyses and influence diagnostics (Cook’s distance, DFBETAS) in metafor to identify influential studies; report material shifts in pooled effect (> 20% change in magnitude or crossing of no‑effect line).

Certainty of the evidence assessment

The formal summary of findings table will prioritise the comparison of any oral melatonin supplementation (IR and CR/SR; all eligible doses pooled) versus placebo or no treatment in adults at the end‑of‑treatment time point.

We will assess the certainty of the evidence for each outcome using the GRADE approach [49]. GRADE considers five domains that may lower certainty (risk of bias, inconsistency, indirectness, imprecision, and publication bias) and, where relevant, three factors that may increase certainty for non‑randomised evidence (large effect, dose‑response gradient, and effect of all plausible residual confounding). Because this review will include randomised trials, we will begin at high certainty for each outcome and downgrade as warranted; upgrading domains rarely apply but will be noted if clearly met (e.g. a consistent dose‑response gradient emerging from our planned DRMA). Two review authors will make domain‑level and overall certainty judgements independently, resolving any differences by discussion or third review author arbitration.

Outcomes to be displayed in the primary summary of findings table

The following outcomes were prioritised a priori for decision‐making and will be displayed in the primary summary of findings table irrespective of data availability (outcomes lacking data will be shown as "no evidence").

1. Change in SBP (mmHg) – critical

2. Change in DBP (mmHg) – critical

3. Change in MAP (mmHg) – important

4. Change in PP (mmHg) – important

5. Change in nocturnal BP dipping (percentage or absolute change) – important

6. Incidence of adverse events (SAEs; and common non‑serious AEs such as headache, dizziness, nausea) – critical for safety

7. Change in QoL (validated scale specified, e.g. SF‑36, EQ‑5D) – important patient‑reported outcome

Additional (supplementary) summary of findings tables

We will prepare additional summary of findings tables only when prespecified subgroup or sensitivity analyses demonstrate clinically important differences (or credible effect modification) and sufficient data exist to support separate ratings. Candidate supplementary tables (subject to data sufficiency) include: (a) melatonin formulation (IR versus CR/SR); (b) baseline BP category (normotensive versus hypertensive); and/or (c) presence versus absence of concomitant antihypertensive medication. Any supplementary summary of findings table will display a restricted outcome set (typically SBP, DBP, and adverse events) to remain within the recommended limits. These additional tables will appear in appendices/Additional tables, not the main summary of findings section, unless requested by the Cochrane Editorial Team.

Judging and presenting certainty ratings

For each outcome, randomised trials start at high‐certainty evidence, which can be downgraded by 0, 1, or 2 levels per domain according to GRADE guidance. We will justify decisions to downgrade the certainty of evidence in footnotes within the GRADEpro GDT‑generated summary of findings table [50]. We will present effect estimates as follows.

• Continuous outcomes (e.g. SBP, DBP, MAP, PP): MD (mmHg) with 95% CI. Where different scales are used (e.g. QoL instruments), we will present SMDs and, where feasible, re‑express SMDs in natural units for interpretability.

• Dichotomous outcomes (e.g. ≥ 1 adverse event; SAEs): RR with 95% CI; absolute risk differences will be derived using baseline risks from representative control groups or pooled control event rates.

We will judge imprecision with reference to optimal information size considerations and clinically important thresholds (e.g. a 5‑millimetres of mercury SBP change). Inconsistency assessments will incorporate both statistical heterogeneity (I², Tau²) and the direction/magnitude of effects across studies (aligned with the heterogeneity plan in Synthesis methods). Publication bias considerations will draw on our ROB‑ME assessment and, when ≥ 10 studies are available, inspection of funnel plots and small‑study effect tests. The influence of missing outcome data will be cross‑linked to RoB 2 domain judgements and incorporated into the overall certainty rating.

We will generate summary of findings tables in GRADEpro GDT [50]. Draft tables will be reviewed by the author team and, if needed, an external GRADE methodologist prior to publication.

Consumer involvement

Direct patient or public involvement in the conduct of this protocol was not feasible. However, we are committed to ensuring that the review addresses patient‑important outcomes and is disseminated in accessible formats. To this end:

• our outcome prioritisation (for the summary of findings table) was informed by clinical experience with patient preferences (BP control, adverse effects, sleep, QoL);

• we will seek informal input on the interpretation and dissemination of review findings from patient advocacy and hypertension support organisations (e.g. national hypertension societies' patient arms, sleep disorder advocacy groups) before final publication;

• plain language summaries and infographics tailored for non‑specialist audiences will be shared through these groups' newsletters, websites, and social media platforms once the review is published.

We will describe in the final review any additional patient or public engagement activities undertaken during the review process.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016159.

Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.

Supplementary material 1 Search strategies

New

Additional information

Contributions of authors

MZ: Lead (conceptualisation, methodology, review, and write‐up)

JM: literature search, methodology, and write‐up

CS: study assessment and write‐up

AP: literature search and write‐up

EP: study assessment and write‐up

AH: contributing to write‐up, reviewing manuscript

Declarations of interest

Muhammad Zia ul Haq has served as a consultant to Switchboard, MD since May 2025 and is a doctoral candidate in the Department of Epidemiology at the University of Michigan.

Javeria Mansoor has declared that they have no conflicts of interest.

Celia C Lima Dos Santos has declared that they have no conflicts of interest.

Aida A Perez Ramos has declared that they have no conflicts of interest.

Emilio Pinzon Cueva has declared that they have no conflicts of interest.

Arash Harzand consults for Switchboard, MD and for the US Centers for Disease Control and Prevention, practises as a staff cardiologist at Emory Healthcare and the Atlanta VA Medical Center, and holds shares and stock options in Moving Analytics and in Switchboard, MD.

All authors have completed Cochrane’s conflict of interest forms.

Sources of support

Internal sources

• No sources of support provided

External sources

• No sources of support provided

Registration and protocol

Cochrane approved the proposal for this review in April 2024.

Data, code and other materials

Data sharing not applicable to this article as it is a protocol, so no datasets were generated or analysed.