Herbal preparations for weight loss in adults

Abstract

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

To assess the effects of herbal preparations for weight loss in adults.

Background

Description of the condition

Obesity and overweight are conditions of increased body weight due to excessive accumulation of body fat. It is estimated that over 1.9 billion adults globally were overweight in 2016, of whom more than 650 million were defined as obese; this represents a three‐fold increase since 1975 (WHO 2018). In the USA, in 2003 and 2004, the prevalence of obesity (body mass index (BMI) greater than or equal to 30 kg/m²) was 32%, whilst 66% were overweight (BMI greater than or equal to 25 kg/m²) (Ogden 2006). In 2015 and 2016, the prevalence of obesity increased to 39.8%. (Hales 2017). By 2008, the medical costs of obesity in the USA amounted to USD 147 billion per year (Finkelstein 2009). In some low‐ or middle‐income countries, the prevalence of obesity has doubled or tripled over the past 10 years, and this has become a critical challenge alongside problems of malnutrition (WHO 2002).

Grades of obesity and overweight are commonly classified using the BMI as the most useful population‐level measure of obesity. This measure is calculated as the body weight (in kilograms) divided by the square of the height (in metres). BMI cut‐off points for the classification of obesity and overweight vary between countries. In the World Health Organization (WHO) definition, a BMI of 25 kg/m² to 29.99 kg/m² is defined as overweight and 30 kg/m² or more as obesity (WHO 2000; WHO 2018). Other important outcome measures include waist circumference and waist‐to‐hip ratio, which reflect abdominal adiposity and indicate the anatomical distribution of body fat. The WHO suggests using both BMI and fat distribution measurements to identify overweight or obese individuals in predicting the risk of cardiovascular disease and diabetes (WHO 2011). Energy intake, expenditure (e.g. physical activity level) and partitioning of nutrient storage are also used as outcome measures (WHO 2000).

The direct cause of obesity and overweight is an imbalance between energy intake and consumption, possibly as a result of excessive intake of foods with poor nutritional value (such as foods with a high content of saturated fats), together with a lack of physical activity. Major individual contributors include genetic, biological (e.g. ethnicity, sex) and 'lifestyle' factors (e.g. smoking, alcohol intake) (Haslam 2005; WHO 2000). Social and environmental influences, such as activity patterns (e.g. sedentary lifestyle), health‐related education and socioeconomic status are important in determining whether individuals develop excessive body weight (Swinburn 2004; Weinsier 1999; WHO 2000).

Obesity and being overweight are risk factors for cardiovascular diseases, particularly coronary heart disease and stroke (Haslam 2005; NIH 1998; WHO 2000; WHO 2018). Other comorbidities include type 2 diabetes, sleep apnoea, musculoskeletal disorders, certain cancers (e.g. breast, ovarian and prostate cancers), gynaecological problems, osteoarthritis, gall bladder disease and psychosocial conditions (NIH 1998; WHO 2000; WHO 2018). As well as reducing the risk of obesity‐associated diseases, achieving a reduction in body weight and ‘successful’ slimming have become extremely popular goals for women and men, including young people, for cosmetic purposes in recent years.

Description of the intervention

Conventional treatments for obesity and overweight include dietary control, physical activity, behaviour modification, pharmacotherapy and surgery (Haslam 2005; NIH 1998; WHO 2000). Surgical treatment is recommended only for people with a BMI greater than 40 kg/m² or a BMI greater than 35 kg/m² with serious comorbid conditions (WHO 2000). In most countries, pharmacological treatment is considered only for people with a BMI of more than 30 kg/m² who fail to respond to dietary management, physical activity and behaviour modification. It is commonly believed that a threshold for weight loss of at least 5% should be considered as clinically significant (Williamson 2015). However, a smaller weight loss may also show beneficial effects for some outcome measurements (Ross 2016; Williamson 2015).

Common pharmaceutical drugs prescribed for obesity in many countries are orlistat (a pancreatic lipase inhibitor), lorcaserin (a serotonin 2C agonist) and phentermine (a noradrenalin releaser) (Adan 2013; Haslam 2005). To date, several pharmaceutical drugs, including fenfluramine, dexfenfluramine and sibutramine, have been prohibited worldwide due to an association with serious adverse cardiac effects, such as stroke and myocardial infarction (Adan 2013).

Due to the unpleasant effects of conventional anti‐obesity drugs, people may seek alternative treatment approaches, including herbal medicines, for achieving weight loss. Herbal preparations for weight loss are popular and can be purchased without prescription from numerous types of retail outlets worldwide, including by mail order and via the Internet. A cross‐sectional study conducted in the UK showed that weight loss and obesity were amongst the conditions most frequently advertised by high‐street 'traditional Chinese medicine' (TCM) shops (Teng 2015). Another study, investigating slimming product advertisements in Switzerland, found that the term 'natural' was claimed by over 90% of slimming products investigated (Droz 2014). A national survey in the USA showed that, compared to non‐obese respondents, people with obesity are more likely to use herbal medicine (Rashrash 2017).

Herbal preparations are used in some countries as part of mainstream health care (e.g. in China and Korea), or due to traditional ethnic influences (e.g. in Singapore), or as 'complementary medicines' (e.g. in the USA, Australia and the UK) (WHO 2013). They are selected either in a conventional Western way, or 'prescribed' in a traditional way (e.g. traditional Chinese medicine, Ayurvedic medicines and some African herbal medicines). Traditional practices for herbal medicines are generally based on the abstract philosophical theory of the domestic medical culture in each country (e.g. TCM in China). Most treatments for traditional use are highly individualised and use abstract 'patterns' to categorise disease.

Adverse effects of the intervention

One of the possible reasons consumers choose herbal medicines for weight loss is that such products are considered (by consumers) to be natural and safe. However, there have been high‐profile safety concerns about herbal weight loss products worldwide (Corns 2002; MHRA 2016; Nortier 2000). For example, herbal slimming products in the UK have been found to contain herbs that are restricted or prohibited, such as ephedra (i.e. Ephedra sinica, commonly known as Ma Huang) and Aristolochia species (e.g. Aristolochia fangchi, A. manshuriensis), or conventional medicines that have prescription‐only status or are prohibited (e.g. fenfluramine).

A cross‐sectional study carried out in the USA in 1998 (Blanck 2001) found that 7% of participants, of whom 5% were of normal weight (BMI below 25 kg/m²), used non‐prescription weight loss products, including liquid meal‐replacement products and products containing chromium picolinate, ephedra and phenylpropanolamine. Over‐the‐counter (OTC) medicines containing ephedra and phenylpropanolamine have been discontinued in many countries due to safety concerns. Products containing ephedrine (an active compound of ephedra) have been banned in the USA since 2004 due to an increase in the risk of stroke, heart attack and other cardiovascular disease (FDA 2004).

Moreover, ingestion of Aristolochia species has resulted in renal (kidney) failure (Lord 1999; Vanherweghem 1998) and renal cancer (Corns 2002; Nortier 2000). Studies assessing the efficacy and safety of ephedra have associated the herb with psychiatric and cardiac problems (Lake 1990; McBride 2004; Shekelle 2003). More recently, reports of hepatotoxicity have emerged following use of products containing brindleberry (also known as malabar tamarind, Garcinia cambogia) (Semwal 2015; Sharma 2018) and following excessive use, or use of concentrated preparations of green tea (Camellia sinensis) extract (Mazzanti 2015).

How the intervention might work

Drugs for weight loss typically work by either reducing energy intake (known as anorectics) or increasing energy expenditure (e.g. fat burning), or both (Adan 2013). For many herbal medicines, these effects have been demonstrated only in preclinical studies.

Ephedra is a well‐known herbal anorectic due to containing ephedrine alkaloids such as ephedrine and pseudoephedrine, which could potentially modulate the central nervous system via stimulating α‐ and β‐adrenoceptors and result in suppressing appetite (Barnes 2007; WHO 1999). Other anti‐obesity mechanisms of ephedrine include thermogenetic effects to burn body fat (WHO 1999) and modulate gut microbiota (Kim 2014; Liu 2017). Ephedra is also found to have increasing activities of peroxisome proliferator activated receptor (PPAR‐α) (Liu 2017).

Green tea is another typical herb used for increasing energy expenditure as it contains catechin polyphenols (Choi 2016; Duloo 2000; Liu 2017). Catechin in green tea could inhibit catechol‐o‐methyltransferase, degrade noradrenalin, extend the stimulation time of the sympathetic nervous system, and therefore increase energy expenditure (Duloo 2000). Catechin is also associated with activating the nuclear factor erythroid 2‐related factor 2 (Nrf2) pathway to inhibit body fat accumulation (Liu 2017). A common herb used in East‐Asian medicine, Chinese goldthread (Coptidis chinensis, also known as Huang Lian), has been found to decrease low‐density lipoprotein cholesterol (LDL‐C) and total cholesterol levels due to the active compound of berberine (Liu 2017; Pirillo 2015).

Preclinical studies by Tian and colleagues showed that several herbs were found to contain active compounds that could inhibit the activity of fatty acid synthase (FAS) in rats. In this study, 17 of 31 Chinese herbs assessed achieved at least 40% inhibition of FAS and nine achieved over 80% inhibition. Active herbs included rhubarb root (Rheum palmatum), a mistletoe plant (Loranthus parasiticus), tuber fleece flower root (Polygonum multiflorum), ginkgo leaf (Ginkgo biloba) and green tea leaf (Camellia sinensis) (Tian 2004).

In East‐Asian medicine, herbal preparations for weight loss usually contain multiple herbs. A traditional Japanese formulae, Bofutsushosan, which contains skullcaps root (Scutellaria baicalensis), Liquorice root (Glycyrrhiza uralensis, G. glabra) and Platycodon root (Platycodon grandiflorus), is commonly prescribed for weight loss in Japan. This preparation may have a thermogenesis effect that increased energy expenditure of rats and suppressed the body weight gain in rats (Takakura 1997). The main mechanism is to increase mRNA expression levels of leptin, adiponectin and uncoupling protein‐1, and result in the decrease of visceral adipocytes and visceral adipose tissue weight (Kobayashi 2017).

Why it is important to do this review

Randomised controlled trials (RCTs) have found that herbal weight loss medicines had positive effects on weight control and were well tolerated (Boozer 2001; Boozer 2002; Park 2013; Sengupta 2012; Stern 2013). Herbs tested in these studies include ephedra (Boozer 2001; Boozer 2002); ben oil tree or moringa (Moringa oleifera), curry tree (Murraya koenigii) and turmeric root (Curcuma longa) (Sengupta 2012); and East Indian globe thistle (Sphaeranthus indicus) and mangosteen (Garcinia mangostana) (Stern 2013). However, the increasing awareness of safety concerns raises questions about the beneficial versus harmful effects of herbal preparations for weight loss. The efficacy and safety of herbal preparations for obesity and overweight have not, to our knowledge, been sufficiently explored in large controlled clinical trials, though this needs to be confirmed by extensive and systematic literature searches. Overall, questions relating to the evidence for herbal weight loss products need to be answered and assessed using a systematic approach.

Several systematic reviews have addressed similar issues. These publications have reviewed the detail and the classification of the types of herbal species used (Esteghamati 2015; Hasani‐Ranjbar 2009; Hasani‐Ranjbar 2013), the effect of single herbs rather than combined herbal formulae (Onakpoya 2011; Shekelle 2003), or they focused on adverse effects only (Pittler 2005; Shekelle 2003). Further, most of these reviews were not reported according to the criteria of the PRISMA statement (Moher 2009).

At present, two Cochrane Reviews have been published assessing ‘herbs', i.e. green tea (Jurgens 2012) and chitosan (Jull 2008), for overweight and obesity. However, green tea and chitosan could be considered (by consumers at least) to be food or dietary supplements rather than herbal preparations for therapeutic uses (though under most regulatory regimes, products making therapeutic claims are considered to be ‘medicines’). Despite this, green tea and chitosan may be included in herbal preparations containing multiple herbs.

In essence, there is a lack of well‐designed systematic reviews focusing on the efficacy and safety of herbal preparations, including both single or multiple herbal formulae, for weight loss. Against this background, this review is proposed, which aims to assess the effects of herbal interventions on body weight in obese and non‐obese adults. The findings of this review may provide useful information for consumers, healthcare professionals and health regulators, and therefore contribute to ensuring effective and safe use of herbal preparations.

Objectives

To assess the effects of herbal preparations for weight loss in adults.

Methods

Criteria for considering studies for this review

Types of studies

We will include RCTs.

Types of participants

We will include any individuals who wish to achieve body weight loss. We will only include studies involving adults (aged over 18 years) in this review.

Many people may choose, or be advised, to attempt weight loss to control the progress of certain chronic conditions. Moreover, people with comorbid conditions may be at greater risk of safety problems associated with herbal medicines, such as herb‐drug interactions. We will include studies involving participants with comorbid disorders, such as diabetes mellitus, where the primary objective or primary outcome measure of the intervention is to achieve a reduction in body weight.

Diagnostic criteria for overweight and obese people

We will define participants with a BMI between 25 kg/m² and 29.9 kg/m² as being overweight, and people with a BMI of 30 kg/m² or greater as obese.

Types of interventions

We plan to investigate the following comparisons of intervention versus control/comparator.

Intervention

• Herbal preparations including either single herbs or multiple herbs. In Asian systems of traditional medicine such as traditional Chinese medicine, the term 'herb' refers to the plant species, as well as to animal parts and minerals.

Comparator

• Placebo

• No treatment

• Conventional pharmaceutical drugs

• Non‐pharmacological treatment including exercise, diet and acupuncture

• A combination of any of the following treatments: herbal preparations with a pharmaceutical drug or a non‐pharmacological treatment

Concomitant interventions will be permitted but must be identical in both the intervention and comparator groups to establish fair comparisons. If a study includes multiple arms, we will include all arms that meet the inclusion criteria for this review.

Minimum duration of intervention

The minimum duration of the intervention will be four weeks.

Minimum duration of follow‐up

The minimum duration of follow‐up will be four weeks.

We will define any follow‐up period going beyond the original time frame for the primary outcome measure as specified in the power calculation of the studies' protocol as an extended follow‐up period (also called open‐label extension study) (Buch 2011; Megan 2012).

Summary of specific exclusion criteria

• Studies involving participants with comorbid disorders where the primary objective or primary outcome measure of the intervention is not to achieve a reduction in body weight.

• Studies in people less than 18 years of age.

Types of outcome measures

We will not exclude a study if it fails to report one or several of our primary or secondary outcome measures. If none of our primary or secondary outcomes is reported in the study, we will not include the study but provide some basic information in the "Characteristics of awaiting classification" table. We will extract the following outcomes, using the methods and time points specified below.

Primary outcomes

• Body weight

• Health‐related quality of life

• Adverse events

Secondary outcomes

• Anthropometric measures other than body weight

• Morbidity

• All‐cause mortality

• Socioeconomic effects

Method of outcome measurement

• Body weight: measured as the change in absolute body weight in kg

• Health‐related quality of life: evaluated by a validated instrument such as EuroQol five dimensions questionnaire (EQ‐5D) or WHO‐Quality of Life‐BREF (WHOQOL‐BREF)

• Adverse events: frequency and type of adverse events such as anorexia, cardiovascular problems, liver toxicity

• Anthropometric measures other than body weight: BMI, change in body weight percentage or body‐fat content

• Morbidity: defined as development of any kind of new‐onset diseases such as diabetes mellitus or cardiac conditions

• All‐cause mortality: defined as death from any cause

• Socioeconomic effects: e.g. direct costs, defined as admission/readmission rates, average length of stay, visits to general practitioner, accident/emergency visits; medication consumption; indirect costs, defined as resources lost due to illness by the participant or their family member

Timing of outcome measurement

• For health‐related quality of life: at the end of the intervention and during follow‐up

• For adverse events and all‐cause mortality: at any time after participants were randomised to intervention/comparator groups

• For all other outcome measures: at a minimum of four weeks after intervention and during follow‐up

Search methods for identification of studies

Electronic searches

We will search the following sources from inception of each database to the date of search and will place no restrictions on the language of publication.

• Cochrane Central Register of Controlled Trials (CENTRAL) via the Cochrane Register of Studies Online (CRSO)

• MEDLINE Ovid (Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE Daily and Ovid MEDLINE; from 1946 onwards)

• Embase (Ovid)

• China Academic Journals Full‐text Database (CJFD), using Chinese and English China Biology Medicine disc (CBMdisc)

• Japanese Ichushi‐Web (Igaku Chuo Zasshi) by Japan Medical Abstracts Society (JAMAS), using Japanese and English

• ClinicalTrials.gov (www.clinicaltrials.gov).

• WHO International Clinical Trials Registry Platform (ICTRP) (www.who.int/trialsearch/).

• Chinese Clinical Trial Registry (ChiCTR) (http://www.chictr.org.cn/abouten.aspx)

• UMIN Clinical Trials Registry (UMIN‐CTR) in Japan (https://www.umin.ac.jp/ctr/)

For detailed search strategies, see Appendix 1. To identify newly published studies,we continuously apply an email alert service for MEDLINE via OvidSP, using the search strategy detailed in Appendix 1.

Searching other resources

We will attempt to identify other potentially eligible studies or ancillary publications by searching the reference lists of retrieved included studies, systematic reviews, meta‐analyses and health technology assessment reports. We will also contact the authors of included studies to obtain additional information on the retrieved studies and establish whether we may have missed further studies.

We will not use abstracts or conference proceedings for data extraction unless full data are available from study authors because this information source does not fulfil the CONSORT requirements (CONSORT 2018; Scherer 2018). We will present information on abstracts or conference proceedings that appear to meet the inclusion criteria for this systematic review in the 'Characteristics of studies awaiting classification' table. We will define grey literature as records detected in ClinicalTrials.gov or the WHO ICTRP.

Data collection and analysis

Selection of studies

Two review authors (LT, LZ) will independently screen the abstract, title, or both, of every record we retrieve in the literature searches. We will obtain the full text of all potentially relevant records. We will resolve any disagreements through discussion or by recourse to a third review author (JB). If we cannot resolve a disagreement, we will categorise the study as 'awaiting classification' and will contact the study authors for clarification. We will present an adapted PRISMA flow diagram to show the process of study selection (Liberati 2009). We will list all articles excluded after full‐text assessment in a 'Characteristics of excluded studies' table and will provide the reasons for exclusion.

Data extraction and management

For studies that fulfil our inclusion criteria, two review authors (LT, LZ) will independently extract key information on participants, interventions and comparators. We will describe interventions and comparators according to the 'template for intervention description and replication' (TIDieR) checklist (Hoffmann 2014; Hoffmann 2017).

We will report data on efficacy outcomes and adverse events using standardised data extraction sheets from the Cochrane Metabolic and Endocrine Disorders Group. We will resolve any disagreements by discussion or, if required, by consultation with a third review author (JB).

We will provide information, including the trial identifier, for potentially relevant ongoing trials in the 'Characteristics of ongoing trials' table and in a joint appendix entitled 'Matrix of study endpoint (publications and trial documents)'. We will attempt to find the protocol for each included study and we will report in a joint appendix the primary, secondary and other outcomes from these protocols, alongside the data from the study publications.

We will email all authors of included studies to enquire whether they would be willing to answer questions regarding their studies. We will present the results of this survey in an appendix. We will thereafter seek relevant missing information on the study from the primary study author(s), if required.

Dealing with duplicate and companion publications

In the event of duplicate publications, companion documents or multiple reports of a primary study, we will maximise the information yield by collating all available data and we will use the most complete dataset aggregated across all known publications. We will list duplicate publications, companion documents, multiple reports of a primary study and trial documents of included trials (such as trial registry information) as secondary references under the study identifier (ID) of the included study. Furthermore, we will also list duplicate publications, companion documents, multiple reports of a study and trial documents of excluded studies (such as trial registry information) as secondary references under the study ID of the excluded study.

Data from clinical trials registers

If data from included studies are available as study results in clinical trials registers, such as ClinicalTrials.gov or similar sources, we will make full use of this information and extract the data. If there is also a full publication of the study, we will collate and critically appraise all available data. If an included study is marked as completed in a clinical trial register but no additional information (study results or publication, or both) is available, we will add this study to the 'Characteristics of studies awaiting classification' table.

Assessment of risk of bias in included studies

Two review authors (LT, LZ) will independently assess the risk of bias of each included study. We will resolve any disagreements by consensus, or by consultation with a third review author (JB). In cases of disagreement, we will consult the rest of the group and make a judgement based on consensus. If adequate information is not available from the publications we will contact study authors for missing data on 'Risk of bias' items.

We will use the Cochrane 'Risk of bias' assessment tool (Higgins 2019b) to assign assessments of low, high or unclear risk of bias (for details see Appendix 2; Appendix 3). We will evaluate individual bias items as described in the Cochrane Handbook for Systematic Reviews of Interventions according to the criteria and associated categorisations contained therein(Higgins 2019b).

Summary assessment of risk of bias

We will present a 'Risk of bias' graph and a 'Risk of bias' summary figure. We will distinguish between self‐reported, investigator‐assessed and adjudicated outcome measures. We will consider the following outcomes as self‐reported.

• Body weight, if measured by study participants

• Health‐related quality of life

• Adverse events

• Anthropometric measures other than body weight, if measured by study participants

We will consider the following outcomes to be investigator‐assessed.

• Body weight, if measured by study personnel

• Adverse events, if measured by study personnel

• Anthropometric measures other than body weight, if measured by study personnel

• Morbidity

• All‐cause mortality

• Socioeconomic effects

Risk of bias for a study across outcomes

Some 'Risk of bias' domains, such as selection bias (sequence generation and allocation sequence concealment), affect the risk of bias across all outcome measures in a study. In the case of a high risk of selection bias, we will mark all endpoints investigated in the associated study as being at high risk. Otherwise, we will not perform a summary assessment of the risk of bias across all outcomes for a study.

Risk of bias for an outcome within a study and across domains

We will assess the risk of bias for an outcome measure by including all entries relevant to that outcome (i.e. both study‐level entries and outcome‐specific entries). We consider low risk of bias to denote a low risk of bias for all key domains, unclear risk to denote an unclear risk of bias for one or more key domains and high risk to denote a high risk of bias for one or more key domains.

Risk of bias for an outcome across studies and across domains

To facilitate our assessment of the quality of evidence for key outcomes, we will assess risk of bias across studies and domains for the outcomes included in the 'Summary of findings' table. We will define the evidence as being at low risk of bias when most information comes from studies at low risk of bias, unclear risk of bias when most information comes from studies at low or unclear risk of bias, and high risk of bias when a sufficient proportion of information comes from studies at high risk of bias.

Measures of treatment effect

When at least two included studies are available for a comparison of a given outcome, we will try to express dichotomous data as a risk ratio (RR) or an odds ratio (OR), with 95% confidence intervals (CIs). For continuous outcomes measured on the same scale (e.g. weight loss in kg) we will estimate the intervention effect using the mean difference (MD) with 95% CIs. For continuous outcomes that measure the same underlying concept (e.g. health‐related quality of life) but use different measurement scales, we will calculate the standardised mean difference (SMD). We will express time‐to‐event data as a hazard ratio (HR) with 95% CIs.

Unit of analysis issues

We will take into account whether randomisation occurred at the level of the participant or cluster, and whether multiple observations were made for the same outcome. If more than one comparison from the same study is eligible for inclusion in the same meta‐analysis, we will either combine groups to create a single pair‐wise comparison, or we will appropriately reduce the sample size so that the same participants do not contribute data to the meta‐analysis more than once (splitting the 'shared' group into two or more groups). Although the latter approach offers some solution for adjusting the precision of the comparison, it does not account for correlation arising from inclusion of the same set of participants in multiple comparisons (Higgins 2019a).

We will attempt to re‐analyse cluster‐RCTs that have not appropriately adjusted for potential clustering of participants within clusters in their analyses. Variance of the intervention effects will be inflated by a design effect. Calculation of a design effect involves estimation of an intracluster correlation coefficient (ICC). We will obtain estimates of ICCs by contacting study authors, or by imputing ICC values using either estimates from other included studies that report ICCs or external estimates from empirical research (e.g. Bell 2013). We plan to examine the impact of clustering by performing sensitivity analyses.

Dealing with missing data

If possible, we will obtain missing data from the authors of included studies. We will carefully evaluate important numerical data such as screened, randomly assigned participants, as well as intention‐to‐treat, as‐treated and per‐protocol populations. We will investigate attrition rates (e.g. dropouts, losses to follow‐up and withdrawals) and we will critically appraise issues concerning missing data and use of imputation methods (e.g. last observation carried forward).

For studies in which the standard deviation (SD) of the outcome is not available at follow‐up or we cannot recreate it, we will standardise by the mean of the pooled baseline SD from studies that report this information. Where included studies do not report means and SDs for outcomes, and we do not receive the requested information from study authors, we will impute these values by estimating the mean and variance from the median, range and size of the sample (Hozo 2005). We will investigate the impact of imputation on meta‐analyses by performing sensitivity analyses, and we will report for every outcome which studies had imputed SDs.

Assessment of heterogeneity

In the event of substantial clinical or methodological heterogeneity, we will not report study results as the pooled effect estimate in a meta‐analysis.

We will identify heterogeneity (inconsistency) by visually inspecting the forest plots and by using a standard Chi² test with a significance level of α = 0.1 (Deeks 2019). In view of the low power of this test, we will also consider the I² statistic — which quantifies inconsistency across studies — to assess the impact of heterogeneity on the meta‐analysis (Higgins 2002; Higgins 2003). When we identify heterogeneity, we will attempt to determine the possible reasons for this by examining individual characteristics of the studies and subgroups.

Assessment of reporting biases

If we include 10 or more studies that investigate a particular outcome, we will use funnel plots to assess small‐study effects. Several explanations may account for funnel plot asymmetry, including true heterogeneity of effect with respect to study size, poor methodological design (and hence bias of small studies) and selective non‐reporting (Kirkham 2010). Therefore we will interpret the results carefully (Sterne 2011).

Data synthesis

We plan to undertake (or display) a meta‐analysis only if we judge the participants, interventions, comparisons and outcomes to be sufficiently similar to ensure a result that is clinically meaningful. Unless good evidence shows homogeneous effects across studies of different methodological quality, we will primarily summarise data that are of low risk of bias using a random‐effects model (Wood 2008). We will interpret random‐effects meta‐analyses with due consideration for the whole distribution of effects and will present a prediction interval (Borenstein 2017a; Borenstein 2017b; Higgins 2009). A prediction interval requires at least three studies to be calculated and specifies a predicted range for the true treatment effect in an individual study (Riley 2013). For rare events (such as event rates below 1%) we will use the Peto odds ratio method, provided there is no substantial imbalance between intervention and comparator group sizes, and intervention effects are not exceptionally large. In addition, we will perform statistical analyses according to the statistical guidelines presented in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2019).

Subgroup analysis and investigation of heterogeneity

We expect the following characteristics to introduce clinical heterogeneity, and we plan to carry out subgroup analyses for these, including investigation of interactions (Altman 2003).

• Types of interventions (e.g. single herbal preparation, multiple herbal preparation)

• Overweight and obesity levels

• Comorbidities/complications (e.g. diabetes mellitus)

Sensitivity analysis

When applicable, we plan to explore the influence of important factors on effect sizes, by performing sensitivity analyses in which we restrict the analyses to the following.

• Published studies.

• Studies with low risk of bias, as specified in the Assessment of risk of bias in included studies section.

• Very long or large studies, to establish the extent to which they dominate the results.

We will use of the following filters, if applicable: diagnostic criteria, imputation used, language of publication (English versus other languages), source of funding (industry versus other), or country (depending on data).

We will also test the robustness of results by repeating the analyses using different measures of effect size (i.e. RR, OR, etc.) and different statistical models (fixed‐effect and random‐effects models).

Certainty of the evidence

We will present the overall certainty of the evidence for each outcome specified below, according to the GRADE approach, which takes into account issues related to internal validity (risk of bias, inconsistency, imprecision, publication bias) and external validity (directness of results). Two review authors (LT, LZ) will independently rate the certainty of evidence for each outcome. We will resolve any differences in assessment by discussion or by consultation with a third review author (JB).

We will include an appendix entitled 'Checklist to aid consistency and reproducibility of GRADE assessments', to help with standardisation of the 'Summary of findings' tables (Meader 2014). Alternatively, we will use GRADEpro GDT software and will present evidence profile tables as an appendix (GRADEpro GDT 2015). If meta‐analysis is not possible, we will present the results in a narrative format in the 'Summary of findings' table. We will justify all decisions to downgrade the certainty of the evidence by using footnotes, and we will make comments to aid the reader's understanding of the Cochrane Review when necessary.

'Summary of findings' table

We will present a summary of the evidence in a 'Summary of findings' table. This will provide key information about the best estimate of the magnitude of the effect, in relative terms and as absolute differences for each relevant comparison of alternative management strategies; the numbers of participants and studies addressing each important outcome; and a rating of overall confidence in effect estimates for each outcome. We will create the 'Summary of findings' table using the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2019), along with Review Manager 5 software (RevMan 2014).

Interventions presented in the 'Summary of findings' tables will be herbal preparations including either single herbs or multiple herbs. The comparators will be placebo, no treatment, conventional pharmaceutical drugs, non‐pharmacological treatment or a combination of any of the following treatments: herbal preparations with a pharmaceutical drug or a non‐pharmacological treatment. We will report the following outcomes, listed according to importance for decision makers.

• Body weight

• Adverse events

• Health‐related quality of life

• Morbidity

• All‐cause mortality

• Anthropometric measures other than body weight (BMI)

• Socioeconomic effects

Notes

We have based parts of the Methods, as well as Appendix 1 and Appendix 3 of this Cochrane protocol, on a standard template established by the CMED group.

Appendices

Appendix 1. Search strategies

MEDLINE (Ovid SP platform): Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE(R) Daily and Ovid MEDLINE(R) 1946 to Present

Search strategy: Herbal medicine 1. exp Herbal Medicine/ 2. exp Plants, Medicinal/ 3. exp Phytotherapy/ 4. exp Herbals as Topic/ 5. exp teas, herbal/ 6. exp Drugs, Chinese Herbal/ 7. exp Medicine, Traditional/ 8. exp Materia Medica/ 9. (herb or herbs or herbal$).tw,kf,ot. 10. materia medica.tw,kf,ot. 11. traditional medic$.tw,kf,ot. 12. traditional drug$.tw,kf,ot. 13. traditional formul$.tw,kf,ot. 14. traditional prescri$.tw,kf,ot. 15. traditional remed$.tw,kf,ot. 16. Chinese medic$.tw,kf,ot. 17. (TCM or TCMs).tw,kf,ot. 18. Chinese drug$.tw,kf,ot. 19. Chinese formul$.tw,kf,ot. 20. Chinese prescri$.tw,kf,ot. 21. Chinese remed$.tw,kf,ot. 22. kampo.tw,kf,ot. 23. or/1‐22 Search strategy for weight loss: 24. exp Obesity/ 25. exp Weight Gain/ 26. exp Weight Loss/ 27. exp Body Mass Index/ 28. exp Skinfold Thickness/ 29. exp Body Fat Distribution/ 30. exp Waist‐Hip Ratio/ 31. exp Abdominal Fat/ 32. exp Overweight/ 33. (overweight or over weight).tw,kf,ot. 34. fat overload syndrom$.tw,kf,ot. 35. (overeat or over eat).tw,kf,ot. 36. (overfeed or over feed).tw,kf,ot. 37. (adipos$ or obes$).tw,kf,ot. 38. (weight adj6 (cyc$ or reduc$ or los$ or maint$ or decreas$ or watch$ or control$ or gain or chang$)).tw,kf,ot. 39. (body mass ind$ or BMI or quetelet ind$).tw,kf,ot. 40. waist‐hip ratio.tw,kf,ot. 41. skinfold thickness.tw,kf,ot. 42. abdominal fat.tw,kf,ot. 43. or/24‐42 RCTs [Cochrane handbook Box 6.4.c: Cochrane Highly Sensitive Search Strategy for identifying randomized trials in MEDLINE: sensitivity‐maximizing version (2008 revision)] 44. randomized controlled trial.pt. 45. controlled clinical trial.pt. 46. randomized.ab. 47. placebo.ab. 48. drug therapy.fs. 49. randomly.ab. 50. trial.ab. 51. groups.ab. 52. or/59‐66 53. exp animals/ not humans.sh. 54. 52 not 53 Retrieving publications: 55. 23 and 43 and 54

Appendix 2. 'Risk of bias' assessment

'Risk of bias' domains

Random sequence generation (selection bias due to inadequate generation of a randomised sequence) For each included study, we will describe the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups. Low risk of bias: study authors achieved sequence generation using computer‐generated random numbers or a random numbers table. Drawing of lots, tossing a coin, shuffling cards or envelopes, and throwing dice are adequate if an independent person performed this who was not otherwise involved in the study. We will consider the use of the minimisation technique as equivalent to being random. Unclear risk of bias: insufficient information about the sequence generation process. High risk of bias: the sequence generation method was non‐random or quasi‐random (e.g. sequence generated by odd or even date of birth; sequence generated by some rule based on date (or day) of admission; sequence generated by some rule based on hospital or clinic record number; allocation by judgement of the clinician; allocation by preference of the participant; allocation based on the results of a laboratory test or a series of tests; or allocation by availability of the intervention). Allocation concealment (selection bias due to inadequate concealment of allocation prior to assignment) We will describe for each included study the method used to conceal allocation to interventions prior to assignment and we will assess whether intervention allocation could have been foreseen in advance of or during recruitment or changed after assignment. Low risk of bias: central allocation (including telephone, interactive voice‐recorder, internet‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes. Unclear risk of bias: insufficient information about the allocation concealment. High risk of bias: used an open random allocation schedule (e.g. a list of random numbers); assignment envelopes used without appropriate safeguards; alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure. We will also evaluate study baseline data to incorporate assessment of baseline imbalance into the 'Risk of bias' judgement for selection bias (Corbett 2014). Chance imbalances may also affect judgements on the risk of attrition bias. In the case of unadjusted analyses, we will distinguish between studies that we rate as being at low risk of bias on the basis of both randomisation methods and baseline similarity, and studies that we judge as being at low risk of bias on the basis of baseline similarity alone (Corbett 2014). We will reclassify judgements of unclear, low, or high risk of selection bias as specified in Appendix 3. Blinding of participants and study personnel (performance bias due to knowledge of the allocated interventions by participants and personnel during the study) We will evaluate the risk of detection bias separately for each outcome (Hróbjartsson 2013). We will note whether endpoints were self‐reported, investigator‐assessed, or adjudicated outcome measures (see below). Low risk of bias: blinding of participants and key study personnel was ensured, and it was unlikely that the blinding could have been broken; no blinding or incomplete blinding, but we judge that the outcome is unlikely to have been influenced by lack of blinding. Unclear risk of bias: insufficient information about the blinding of participants and study personnel; the study does not address this outcome. High risk of bias: no blinding or incomplete blinding, and the outcome is likely to have been influenced by lack of blinding; blinding of study participants and key personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding. Blinding of outcome assessment (detection bias due to knowledge of the allocated interventions by outcome assessment) We will evaluate the risk of detection bias separately for each outcome (Hróbjartsson 2013). We will note whether endpoints were self‐reported, investigator‐assessed, or adjudicated outcome measures (see below). Low risk of bias: blinding of outcome assessment is ensured, and it is unlikely that the blinding could have been broken; no blinding of outcome assessment, but we judge that the outcome measurement is unlikely to have been influenced by lack of blinding. Unclear risk of bias: insufficient information about the blinding of outcome assessors; the study did not address this outcome. High risk of bias: no blinding of outcome assessment, and the outcome measurement was likely to have been influenced by lack of blinding; blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement was likely to be influenced by lack of blinding. Incomplete outcome data (attrition bias due to quantity, nature or handling of incomplete outcome data) For each included study or each outcome, or both, we will describe the completeness of data, including attrition and exclusions from the analyses. We will state whether the study reported attrition and exclusions, and we will report the number of participants included in the analysis at each stage (compared with the number of randomised participants per intervention/comparator groups). We will also note if the study reported the reasons for attrition or exclusion, and whether missing data were balanced across groups or were related to outcomes. We will consider the implications of missing outcome data per outcome such as high dropout rates (e.g. above 15%) or disparate attrition rates (e.g. difference of 10% or more between study arms). Low risk of bias: no missing outcome data; reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to introduce bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk was not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, plausible effect size (mean difference or standardised mean difference) among missing outcomes was not enough to have a clinically relevant impact on observed effect size; appropriate methods, such as multiple imputation, were used to handle missing data. Unclear risk of bias: insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias; the study did not address this outcome. High risk of bias: reason for missing outcome data was likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in the intervention effect estimate; for continuous outcome data, plausible effect size (mean difference or standardised mean difference) among missing outcomes enough to induce clinically relevant bias in observed effect size; 'as‐treated' or similar analysis done with substantial departure of the intervention received from that assigned at randomisation; potentially inappropriate application of simple imputation. Selective reporting (reporting bias due to selective outcome reporting) We will assess outcome reporting bias by integrating the results of the appendix 'Matrix of study endpoints (publications and trial documents)' (Boutron 2014; Jones 2015; Mathieu 2009), with those of the appendix 'High risk of outcome reporting bias according to the Outcome Reporting Bias In Trials (ORBIT) classification' (Kirkham 2010). This analysis will form the basis for the judgement of selective reporting. Low risk of bias: the study protocol was available and all the study's prespecified (primary and secondary) outcomes that were of interest to this review were reported in the prespecified way; the study protocol was unavailable, but it was clear that the published reports included all expected outcomes (ORBIT classification). Unclear risk of bias: insufficient information about selective reporting. High risk of bias: not all the study's prespecified primary outcomes were reported; one or more primary outcomes were reported using measurements, analysis methods, or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting was provided, such as an unexpected adverse effect); one or more outcomes of interest in the Cochrane Review were reported incompletely so that we cannot enter them into a meta‐analysis; the study report failed to include results for a key outcome that we would expect to have been reported for such a study (ORBIT classification). Other bias Low risk of bias: the study appears to be free from other sources of bias. Unclear risk of bias: information was insufficient to assess whether an important risk of bias existed; there was insufficient rationale or evidence that an identified problem introduced bias. High risk of bias: the study had a potential source of bias related to the specific study design used; the study was claimed to be fraudulent; or the study had some other serious problem.

Appendix 3. Selection bias decisions

Selection bias decisions for studies that reported unadjusted analyses: comparison of results obtained using method details alone versus results obtained using method details and study baseline informationa
Reported randomisation and allocation concealment methods	'Risk of bias' judgement using methods reporting	Information gained from study characteristics data	'Risk of bias' using baseline information and methods reporting
Unclear methods	Unclear risk	Baseline imbalances present for important prognostic variable(s)	High risk
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited or no baseline details	Unclear risk
Would generate a truly random sample, with robust allocation concealment	Low risk	Baseline imbalances present for important prognostic variable(s)	Unclear riskb
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited baseline details, showing balance in some important prognostic variablesc	Low risk
		No baseline details	Unclear risk
Sequence is not truly randomised or allocation concealment is inadequate	High risk	Baseline imbalances present for important prognostic variable(s)	High risk
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited baseline details, showing balance in some important prognostic variablesc	Unclear risk
		No baseline details	High risk
aTaken from Corbett 2014; judgements highlighted in bold indicate situations in which the addition of baseline assessments would change the judgement about risk of selection bias compared with using methods reporting alone. bImbalance was identified that appears likely to be due to chance. cDetails for the remaining important prognostic variables are not reported.

Contributions of authors

All review authors read and approved the final protocol draft.

Sources of support

Internal sources

• None, Other.

• University of Auckland, New Zealand.

  Jo Barnes has received a small research grant from the University of Auckland School of Pharmacy Performance‐Based Research Fund to support a research assistant (E Lyn Lee) to assist with this systematic review.

External sources

• None, Other.

Declarations of interest

Lida Teng (LT): LT is named on the research grant application from the University of Auckland to support ELL to assist with this systematic review.
 Li Zhang (LZ): none known.
 Joanne Barnes (JB): JB has received a small research grant from the University of Auckland to support a research assistant (E Lyn Lee) to assist with this systematic review. She has received travel expenses from academic and charitable organisations to support attendance at academic meetings, royalties from a scientific publishing company in respect of part authorship of an academic textbook, and holds several leadership roles (unpaid) in organisations concerned with pharmacovigilance for medicines, including herbal and traditional medicines.
 E Lyn Lee (ELL): ELL has received a research grant from the Univeristy of Auckland for this systematic review.

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