Treat‐to‐target strategies for low‐density lipoprotein cholesterol and triglyceride levels for primary and secondary prevention of cardiovascular disease in adults with dyslipidaemia

Objectives

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

To evaluate the benefits and harms of a treat‐to‐target (goal‐directed) strategy versus a no‐target strategy for lipid‐lowering therapy in the primary and secondary prevention of cardiovascular disease in adults with dyslipidaemia.

Background

Description of the condition

Cardiovascular disease (CVD) (disorders of the heart and blood vessels) is the leading cause of mortality worldwide and a significant contributor to disability [1]. Recent global estimates were approximately 19.2 million CVD deaths in 2023 and about 437 million CVD disability‐adjusted life‐years (DALYs), highlighting the magnitude and ongoing increase of this disease burden [1]. Dyslipidaemia is defined as elevated low‐density lipoprotein cholesterol (LDL‐C) and/or triglycerides, often accompanied by low high‐density lipoprotein cholesterol (HDL‐C). It is prevalent globally and is a well‐established, modifiable risk factor for atherosclerotic CVD (ASCVD), which refers to CVD that results from the build‐up of fatty deposits (plaques) in the arteries. A recent global systematic review of observational studies in adult general populations estimated a pooled prevalence of 18.9% for high levels of LDL‐C and 28.8% for hypertriglyceridemia (elevated blood triglyceride levels), with considerable variation by sex and geographical location [2]. Dyslipidaemia frequently co‐occurs with other major risk factors for ASCVD, such as hypertension, diabetes, and tobacco use. Consequently, CVD prevention strategies, particularly in primary care, are commonly structured around absolute risk assessment (an estimate of an individual’s probability of experiencing a cardiovascular event within a specified period) to inform treatment intensity and prioritisation [3, 4, 5].

Description of the intervention and how it might work

In clinical practice, management of dyslipidaemia generally includes lifestyle or health behaviour modification and, when indicated according to individual cardiovascular risk and lipid levels, lipid‐lowering therapy [5]. Lipid‐lowering therapies are pharmacological treatments used to manage dyslipidaemia by reducing levels of lipids in the blood, particularly LDL‐C and triglycerides. Examples include statins, ezetimibe, PCSK9‐targeting therapies, bempedoic acid, fibrates, bile acid sequestrants, and combination therapies. Different approaches have been used to guide initiating and adjusting lipid‐lowering therapy, including treat‐to‐target and no‐target strategies, which are compared in this review.

In treat‐to‐target (goal‐directed) strategies, clinicians initiate lipid‐lowering therapy and then use repeated lipid measurements to determine whether a predetermined lipid goal—most commonly an LDL‐C goal—has been achieved [4, 6]. If this goal is not achieved, treatment is intensified, for example, by increasing the dose or adding another lipid‐lowering agent, with the aim of further reducing lipid levels, and thereby, reducing cardiovascular risk [4]. Treat‐to‐target strategies may also differ in the lipid target pursued, such as lower (more intensive) and higher (less intensive) prespecified lipid targets.

In contrast, in a no‐target strategy, a recommended drug class and/or statin intensity is prescribed based on baseline cardiovascular risk and clinical profile, without defining therapeutic success as the attainment of a specific LDL‐C target [3]. In this paradigm, follow‐up lipid testing is still used, but its primary role is to assess adherence and the adequacy of treatment response (often expressed as a percentage LDL‐C reduction), and to support shared decisions about whether therapy should be continued, intensified, or modified [3, 4, 7]. Some clinical guideline groups have concluded that much of the randomised trial evidence demonstrating clinical benefit was based on fixed‐dose or fixed‐intensity statin regimens [8, 9]. They also judge that this evidence does not provide adequate direct support for titrating therapy to achieve specific LDL‐C targets. Consequently, the guidelines emphasise initiating an appropriate statin intensity and monitoring treatment response primarily for adherence and safety, and to judge whether the expected LDL‐C response has been achieved. In some frameworks, specified on‐treatment LDL‐C levels are used as thresholds for considering additional lipid‐lowering therapy (add‐on therapy) in people at high risk of cardiovascular events [3, 9, 10].

These strategies therefore differ not only in the metric used to judge treatment response (goal attainment versus intensity/percentage reduction and thresholds), but also in the broader 'package' of care they imply—such as the frequency of lipid testing and follow‐up, the explicitness of intensification rules, and access to additional lipid‐lowering agents. These differences in lipid‐lowering strategies may influence achieved lipid levels, the likelihood of treatment intensification and combination therapy, adherence and persistence, the occurrence of adverse effects, and health‐system resource use. Their effects may also vary according to patient characteristics that influence baseline cardiovascular risk, lipid levels, or response to treatment, including age, sex, metabolic disorders, chronic kidney disease, and HIV status. Differences in thresholds for initiating treatment and the type of lipid‐lowering therapy used may also modify the effect of these strategies. In addition, their implementation may vary across settings with different capacities for laboratory monitoring and medicine availability [4, 11, 12].

Why it is important to do this review

As the World Health Organisation (WHO) develops a global guideline for dyslipidaemia management in both primary prevention (prevention of a first cardiovascular event) and secondary prevention (prevention of further cardiovascular events in people with established CVD), policymakers require robust evidence regarding whether a treat‐to‐target strategy, which involves titrating therapy to achieve lipid goals, confers meaningful advantages over a no‐target approach, which uses fixed‐dose or intensity treatment without pursuing specific numerical goals. This question is critical not only because the two strategies may differ in patient‐important outcomes, such as mortality and major cardiovascular events, but also because they entail different requirements for laboratory monitoring, clinical follow‐up, and access to add‐on therapies [13]. These factors may influence feasibility and equity across health systems.

Existing evidence syntheses have mainly evaluated the efficacy and safety of lipid‐lowering drugs, statin intensity, or alternative LDL‐C‐lowering regimens, rather than directly comparing target‐based lipid‐management strategies with non‐target‐based strategies across primary and secondary prevention populations. To our knowledge, no systematic review directly addresses the comparative benefits and harms of treat‐to‐target versus no‐target lipid‐management strategies. A recent individual participant data meta‐analysis evaluated alternative LDL‐C‐lowering strategies versus high‐intensity statins in people with established ASCVD, but this does not address the broader question of target‐based versus no‐target strategies across prevention settings, lipid targets, and healthcare contexts [14].

This review forms part of a suite of policy‐focused Cochrane reviews commissioned by the WHO to inform their guideline panel by providing the best available comparative evidence on the benefits and harms of treat‐to‐target versus no‐target lipid management strategies. As these reviews address related questions within a common evidence synthesis framework, some sections of the Background and Methods are similar across protocols.

Objectives

To evaluate the benefits and harms of a treat‐to‐target (goal‐directed) strategy versus a no‐target strategy for lipid‐lowering therapy in the primary and secondary prevention of cardiovascular disease in adults with dyslipidaemia.

Methods

We will report this protocol according to Preferred Reporting Items for Systematic review and Meta‐Analysis‐Protocols (PRISMA‐P) [15], conduct the review following the Cochrane Handbook for Systematic Reviews of Interventions [16] and the Methodological Expectations for Cochrane intervention reviews (MECIR) guidance [17], and report the completed review following PRISMA 2020 [18].

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs), both individually randomised and cluster‐randomised, that compare a treat‐to‐target strategy with a no‐target strategy for lipid management in adults with dyslipidaemia. We will include full‐text publications and preprints when sufficient information is available on design, participants, interventions, and outcomes; we will not restrict eligibility by publication year, language, or publication status.

We will exclude cross‐over trials because lipid management may have sustained effects on treatment exposure and lipid levels, and outcomes such as cardiovascular events are not reversible; therefore, carry‐over and contamination across periods are likely [19, 20]. We will also exclude quasi‐randomised studies (e.g. allocation by date of birth, record number, or alternation) because of the high risk of selection bias. We will exclude reports that do not provide adequate data for eligibility assessment or outcome extraction (e.g. conference abstracts without sufficient trial details).

If the available RCTs address the review question indirectly or incompletely, we will consider including controlled non‐randomised studies of interventions (NRSIs), in accordance with the Cochrane Handbook for Systematic Reviews of Interventions [21, 22]. RCTs will remain the primary source of evidence. We will consider NRSIs only where the available RCT evidence does not adequately address a specific PICO question, for example, because relevant long‐term outcomes are not reported, or the implementation of the treat‐to‐target strategy does not adequately reflect our predefined intervention of interest. We will not include NSRIs solely because the number of available RCTs is small, or their effect estimates are imprecise. We will characterise eligible NRSI according to key design features, rather than study design labels alone. Eligible studies must compare a treat‐to‐target lipid management strategy with an eligible no‐target strategy and allow the estimation of the effect of assignment to, or initiation of, these strategies. We further require a clearly defined intervention and comparator, a defined start of follow‐up in relation to assignment or initiation of the intervention strategies, and a contemporaneous comparison group. We will exclude NSRIs without an eligible comparison group, uncontrolled interrupted time‐series, case reports, case series, and cross‐sectional analyses [21, 22].

We will initially consider including NRSIs of 800 or more participants [22]. If no relevant evidence is available from RCTs or NRSIs with 800 or more participants for a specific review question, we will extend eligibility to NRSIs including between 400 and 800 participants [22]. Any further restrictions on which eligible NRSIs will be included in our synthesis, for example, based on risk of bias, will be jointly discussed with the Cochrane Methods Support Unit and with members of the WHO guideline panel.

Types of participants

We will include adults (≥ 18 years) at risk of cardiovascular disease, and will include both primary and secondary CVD prevention populations. We will conduct separate analyses for primary and secondary prevention populations.

We will define secondary prevention as participants with established clinical atherosclerotic cardiovascular disease at baseline, including previous myocardial infarction, acute coronary syndrome, coronary revascularisation, angina or coronary heart disease, ischaemic stroke or transient ischaemic attack, symptomatic peripheral artery disease, or clinically diagnosed aortic atherosclerotic disease. Primary prevention will be defined as participants eligible for lipid‐lowering therapy because of dyslipidaemia, familial hypercholesterolaemia, or calculated cardiovascular risk, and who do not have established clinical atherosclerotic cardiovascular disease at baseline.

We will include studies conducted in any country and setting. For studies enrolling mixed primary and secondary prevention populations, we will extract prevention‐stratum‐specific results when reported. If stratified results are not provided, we will contact study authors to request these data. If stratified results remain unavailable, we will include the study in the relevant prevention stratum only if at least 80% of participants are in that stratum; otherwise, the study will not be included in the quantitative synthesis for prevention‐specific analyses.

We will exclude studies restricted to children or adolescents (i.e. less than 18 years of age). For studies that include both adults and participants aged under 18, we will include the study only if adult‐only data are available or if at least 80% of participants are adults or subgroups are reported; otherwise, we will exclude the study.

Types of interventions

We will include studies that compare different lipid‐management strategies for adults receiving pharmacological lipid‐lowering therapies (LLT), including statin and non‐statin therapies, where the intervention and comparator differ in whether treatment is adjusted during follow‐up to achieve a prespecified lipid target. We will exclude studies evaluating multifactorial target‐based interventions in which treatment is simultaneously titrated to achieve non‐lipid targets, such as blood pressure and blood glucose level.

Intervention (treat‐to‐target/goal‐directed strategy)

We will include target‐based lipid management strategies in which LLT is initiated and titrated according to a prespecified lipid target, with lipid levels monitored during follow‐up and treatment adjusted to achieve that goal. The timing and frequency of lipid monitoring may vary between strategies. Strategies may include statin dose titration and/or the addition of other lipid‐lowering agents, as needed, to reach the goal. The prespecified goal may be expressed as an LDL‐C threshold or range (including mmol/L equivalents), and may also include prespecified triglyceride targets when the strategy is explicitly goal‐directed. For synthesis, we will classify LDL‐C targets using the following categories.

Primary target definition

• LDL‐C target < 70 mg/dL (including targets expressed as < 70 mg/dL or ranges centred on 70 mg/dL, e.g. 50 to 70 mg/dL), as the main reference category for synthesis

Other targets (handled as subgroups/effect modifiers, not separate primary comparisons)

• More intensive LDL‐C targets (e.g. < 55 mg/dL or < 40 mg/dL)

• Less intensive LDL‐C targets (e.g. < 100 mg/dL or 90 to 110 mg/dL)

• Triglyceride targets (e.g. < 150 mg/dL or < 200 mg/dL) where the intervention is explicitly target‐based

Comparator (no‐target strategy)

We will include no‐target (non–goal‐directed) strategies in which LLT is prescribed as a fixed‐dose or intensity‐based approach (including usual care as defined by trial authors) without a requirement to achieve a numerical lipid goal. Lipid testing may be performed for adherence or safety monitoring, but treatment escalation is not conducted with the explicit aim of attaining a prespecified lipid target.

Additional eligible comparisons

We will also include studies that directly compare lower versus higher lipid target thresholds within goal‐directed strategies (i.e. both arms are treat‐to‐target but with different targets) or trials that compare a single target or no target with a strategy using different prespecified lipid targets according to the participants' baseline characteristics, such as baseline LDL‐C level. We will analyse these comparisons separately from the primary treat‐to‐target versus no‐target comparison.

We will not restrict eligibility by the specific dose, dosing frequency, or drug class of lipid‐lowering therapy, provided that the comparison is between the above‐described management strategies and that sufficient detail is available to classify the intervention and comparator. We will not apply a minimum follow‐up duration for eligibility, but we will group outcome data according to the prespecified follow‐up categories (see 'Time points' below).

Outcome measures

We will not restrict study eligibility based on the outcomes assessed or reported by the studies.

Critical outcomes

• All‐cause mortality: death from any cause during the study follow‐up period

• Atherosclerotic cardiovascular disease (ASCVD) death: death attributable to atherosclerotic vascular causes, such as fatal myocardial infarction or ischaemic stroke

• 3‐point major adverse cardiovascular events (MACE): a composite outcome consisting of non‐fatal myocardial infarction, non‐fatal stroke, or cardiovascular death

• Stroke or transient ischaemic attack: a new (non‐fatal) focal neurological event due to cerebrovascular ischaemia or haemorrhage, including transient symptoms resolving fully within 24 hours (TIA (transient ischaemic attack))

• Coronary heart disease: a disease caused by the narrowing or blockage of the coronary arteries that can present as myocardial infarction, angina syndromes, or the need for coronary revascularisation.

• Aortic atherosclerotic disease: atherosclerotic involvement of the aorta leading to clinically relevant conditions such as aortic aneurysm, aortic dissection, or symptomatic/treated aortic plaque

• Peripheral artery disease: atherosclerotic disease of non‐coronary, non‐cerebral arteries—typically lower‐limb arteries—causing symptoms, abnormal perfusion indices, or limb events/procedures

Important outcomes

• Muscle symptoms: muscle pain, cramps, weakness, or stiffness occurring during statin therapy with no alternative clear cause, regardless of creatine kinase level

• Hepatotoxicity (liver enzyme elevation): an increase in hepatic transaminases (ALT or AST or both) during therapy that meets the study’s prespecified definition of a clinically meaningful elevation and, where reported, is considered by the study investigators to be potentially attributable to the study drug

• Myopathy/myositis/rhabdomyolysis: muscle toxicity ranging from symptomatic myositis or weakness to rhabdomyolysis, typically defined by symptoms or substantial creatine kinase elevation (or both) and, in severe cases, kidney injury

• Medication adherence: the extent to which participants take the assigned lipid‐lowering therapy as prescribed over the follow‐up period

• Pancreatitis: an acute episode of pancreatic inflammation identified by compatible clinical features and supported by elevated pancreatic enzymes and/or imaging

• New‐onset diabetes mellitus: diabetes first diagnosed after randomisation during follow‐up, as defined within each trial (for example by diagnostic glycaemic criteria or initiation of glucose‐lowering therapy)

Outcome measurement hierarchy

If studies report the same outcome using multiple definitions or methods (such as events independently adjudicated against predefined criteria versus events reported without such adjudication, or composite outcomes combining different clinical events), we will select one definition for analysis. We will prioritise clinically adjudicated outcomes and the study’s prespecified outcome definition. If more than one eligible definition remains, we will select the one that is most consistently reported across studies. When both a composite outcome (e.g. 3‐point MACE) and its individual components (such as stroke) are reported, we will extract the composite and its components as separate outcomes. We will not construct composite outcomes by combining individual components reported by a study.

Time points

For synthesis and presentation, we will group follow‐up into the following categories.

• Short term: up to and including 12 months

• Medium term: from 12 to 36 months

• Long term: more than 36 months

We will extract one time point per study within each follow‐up category. If a study reports multiple time points within a category, we will use the latest time point within that category.

Search methods for identification of studies

Electronic searches

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

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

• MEDLINE (Ovid; ALL 1946 to date of search)

• Global Health (Ovid; 1973 to date of search)

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (https://www.clinicaltrials.gov)

• World Health Organization International Clinical Trials Registry Platform (ICTRP) (https://www.who.int/trialsearch/)

The details of the search strategies can be found in Supplementary material 1.

We used the following search filters to identify randomised and non‐randomised clinical trials: Cochrane Highly Sensitive Search Strategy for identifying randomised trials in (Medline Ovid): sensitivity‐maximizing version (2023 revision) [23] and Search filter with best specificity for controlled NRS (Medline Ovid) [24]. The search strategy was peer‐reviewed by an independent information specialist who followed the PRESS guidelines [25].

Searching other resources

We will search the reference lists of all included studies for information about any additional studies.

We will assess whether any included studies have amendments, corrections, or retractions via PubMed, CENTRAL, and Retraction Watch (https://retractiondatabase.org/RetractionSearch.aspx).

Data collection and analysis

Selection of studies

After duplicate records are removed, we will use Covidence to manage the screening process [26]. Two review authors will screen the titles and abstracts independently to determine the eligibility of the studies. We will then obtain the full text for any record considered potentially eligible by either review author. Two review authors will independently assess the full‐text reports against the prespecified eligibility criteria, following the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions [16]. We will conduct this process for both RCTs and NRSIs. During the screening process, all disagreements will be resolved through discussion and, if necessary, by involving a third review author. We will document the study selection process in a PRISMA flow diagram, and we will record the reasons for exclusion at the full‐text stage [18].

Data extraction and management

We will pilot the extraction form on a small sample of included studies (at least three studies) and refine it as needed. Disagreements will be resolved by discussion; if required, a third review author will arbitrate.

We will assess the use of a large language model (Claude, Anthropics) [27] for the extraction of study characteristics and outcomes by performing a Study Within a Review (SWAR) on 10% of the included studies (see protocol in Supplementary material 2). If the evaluation is successful as per the criteria specified in the protocol, we will conduct a semi‐automated data extraction using artificial intelligence (AI) and human verification workflow on the rest of the included studies. If this evaluation does not meet the predefined benchmarks, two review authors will independently extract data from each included study using piloted, standardised data extraction forms.

To ensure consistent capture of intervention details (lipid target, schedule of lipid monitoring, rules used to guide treatment adjustment, and lipid‐lowering therapies permitted for treatment intensification or as add‐on therapy), we will extract intervention characteristics using an adapted TIDieR (Template for Intervention Description and Replication) checklist [28].

When essential information is missing, unclear, or reported in a manner that prevents us from including study results in analyses, we will contact study investigators to request clarification or additional data. For reports requiring translation, we will translate sections relevant to eligibility and data extraction using a native speaker or professional translation where available; if necessary, we will use software‐assisted translation to aid extraction and will document the approach we use.

Data extraction items

For each included study, we will extract the following information.

• Study details: design (including cluster features where applicable), setting, country/region, recruitment period, duration of follow‐up, trial registration (when available)

• Participant details: eligibility criteria, primary versus secondary prevention status at baseline, baseline cardiovascular risk (when reported), baseline lipid values, key comorbidities relevant to prespecified subgroup analyses

• Intervention and comparator characteristics (TIDieR‐informed) [28]: lipid goal definition (including units and threshold/range), monitoring frequency, intensification/titration algorithm, LLT classes and intensity/dose used, duration of treatment, background/concomitant therapies, any adherence‐support components

• Outcome data: outcome definitions and time points. For each outcome domain, we will seek all results compatible with that domain; where multiple measures, analyses, or time points are reported, we will apply prespecified selection rules (e.g. longest follow‐up for the main analysis) and document our decisions.

• Other information: funding source(s) and reported conflicts of interest

We will transform extracted results into formats suitable for meta‐analysis using methods recommended in the Cochrane Handbook [16]. For continuous outcomes, where required, we will derive standard deviations from standard errors, confidence intervals, or other summary statistics using Cochrane‐recommended approaches [29]. For dichotomous outcomes, we will extract the number of participants with events and the number analysed in each arm, preferentially using intention‐to‐treat denominators where available.

Risk of bias assessment in included studies

We will assess the risk of bias in included studies in accordance with the Cochrane Handbook [30].

We will assess the use of a large language model (Claude, Anthropics) for the assessment of risk of bias following the same approach previously mentioned for data extraction (see protocol in Supplementary material 2). If the evaluation is successful as per the criteria specified in the protocol, we will conduct a semi‐automated risk of bias assessment using AI and human verification workflow on the rest of the included studies. If this evaluation does not meet the predefined benchmarks, two review authors will independently assess the risk of bias for each included study. Disagreements will be resolved by discussion and, if needed, by consultation with a third review author.

For individually randomised RCTs, we will use the Cochrane risk of bias tool RoB 2 [31, 32] Our primary interest is the effect of assignment to the intervention (the intention‐to‐treat effect). We will assess the following RoB 2 domains:

• bias arising from the randomisation process;

• bias due to deviations from intended interventions;

• bias due to missing outcome data;

• bias in measurement of the outcome;

• bias in selection of the reported result.

For cluster‐randomised trials, we will use the RoB 2 variant for cluster‐randomised trials and consider additional issues related to recruitment timing, baseline imbalance, and loss of clusters, as recommended in the Cochrane Handbook [19].

For each prespecified outcome assessed for risk of bias, we will apply the RoB 2 algorithms to derive domain‐level judgements (“low risk of bias”, “some concerns”, or “high risk of bias”) and an overall risk of bias judgement for each result.

If we include NRSIs, we will assess their risk of bias using ROBINS‐I (v2) [33] Two review authors will independently assess bias in the following domains:

• bias due to confounding. Potential confounders identified a priori include age, sex, total cholesterol, LDL cholesterol, HDL cholesterol, smoking, blood pressure/hypertension, and diabetes, consistent with major cardiovascular risk prediction models (e.g. QRISK3 [34] or Reynolds Risk Score [35]). Additional confounders that may also be important include deprivation/socioeconomic status, obesity, family history of premature cardiovascular disease, chronic kidney disease, autoimmune disease, HIV, and severe mental illness;

• bias in classification of interventions;

• bias in selection of participants into the study (or into the analysis);

• bias due to missing data;

• bias in measurement of the outcome;

• bias in selection of the reported result.

For each prespecified outcome assessed for risk of bias, we will apply the ROBINS‐I algorithms to derive domain‐level judgements (“low”, “moderate”, “serious”, “critical”, or “no information”) and an overall risk of bias judgement for each result.

For each eligible comparison (treat‐to‐target versus no‐target lipid‐lowering strategies and, if applicable, lower versus higher lipid targets), we will assess risk of bias for all critical and important outcomes at the medium‐term time point (> 12 to 36 months). Where more than one result is available within this timeframe, we will assess the latest available result. If no medium‐term result is available, we will assess the result at the longest available follow‐up and indicate the corresponding timeframe.

Measures of treatment effect

We will extract and analyse outcome data in accordance with Chapter 6 of the Cochrane Handbook [29].

For dichotomous outcomes, such as all‐cause mortality, ASCVD death, 3‐point MACE, stroke/TIA, coronary heart disease events, peripheral artery disease events, pancreatitis, new‐onset diabetes, and myopathy/rhabdomyolysis, we will summarise treatment effects using risk ratios (RRs) with 95% confidence intervals (CIs). Where studies report odds ratios (ORs), we will extract them and, where appropriate and feasible, re‐express them to a common effect measure for synthesis (e.g. convert OR to RR using an assumed comparator risk); if conversion is not appropriate, we will pool ORs separately [29, 36]. If time‐to‐event effect estimates, such as hazard ratios, are reported and represent the most appropriate summary measure for a given outcome, these will be extracted and synthesised separately using the generic inverse‐variance method.

For continuous outcomes, such as lipid levels analysed as continuous variables, we will record the mean, standard deviation (SD), and number of participants analysed in each group. When outcomes are measured on the same scale, we will use the mean difference (MD) with 95% CIs. When the same outcome domain is measured using different scales or instruments, we will apply the standardised mean difference (SMD) with 95% CIs.

When end‐of‐follow‐up (post‐intervention) and change‐from‐baseline values are reported for the same continuous outcome, we will use post‐intervention values preferentially to ensure consistency across studies.

We will consider Peto odds ratios only for very rare events and when treatment groups are balanced. In all other cases, we will use risk ratios (RR) as described above.

We will use prespecified minimally important differences (MIDs) to aid interpretation of the effects on our critical and important outcomes. The proposed selected MID values are presented in Supplementary material 3. When no established MID is available for a continuous outcome, we will interpret the effect sizes using conventional benchmarks for SMD (0.2 point difference) [36].

Unit of analysis issues

We will address all unit of analysis issues in accordance with Chapter 6 of the Cochrane Handbook and the guidance on trial variants in Chapter 23 [19, 29].

For cluster‐randomised trials, we will use methods recommended in the Cochrane Handbook to account for clustering in the analysis [19]. Where study authors have used appropriate methods to adjust for clustering, we will extract the adjusted effect estimates and incorporate them using generic inverse‐variance methods. If clustering has not been accounted for, we will apply approximate methods (effective sample size or inflated standard errors) using an intraclass correlation coefficient (ICC); where ICCs are not reported, we will seek them from authors or use external estimates and explore alternative ICC values in sensitivity analyses.

For trials with three or more eligible arms, we will avoid double‐counting by combining relevant intervention arms where appropriate, or by splitting the shared comparator group across comparisons, following Cochrane guidance for multi‐arm trials [19].

Dealing with missing data

We will contact the study authors to request missing or unclear information. Where outcome data remain unavailable, we will use available‐case analysis and will not impute missing outcome data unless prespecified and justified.

Where appropriate, we will assess the potential impact of missing data on effect estimates through sensitivity analyses, for example, by comparing analyses that include all eligible studies with analyses restricted to studies judged at low risk of bias due to missing outcome data. We will discuss the direction and likely magnitude of any bias introduced by missing data and its implications for the certainty of the evidence

Reporting bias assessment

We will assess the risk of bias due to missing results (reporting biases) in accordance with Chapter 13 of the Cochrane Handbook [37]. At least two review authors will independently assess the risk of bias for each main synthesis; disagreements will be resolved by discussion or, if needed, by consultation with a third review author.

To help identify potentially unpublished or selectively reported results, we will compare outcomes and time points reported in published articles with trial registrations and available protocols where possible, and we will search trial registries (e.g. ClinicalTrials.gov and WHO ICTRP) for completed but unpublished eligible studies. Where relevant information is unclear, we will contact the study authors.

If at least 10 studies are included in a meta‐analysis, we will assess funnel plot asymmetry visually and, where appropriate, use a prespecified statistical test suited to the outcome type and effect measure, such as Egger’s test and Harbord or Peters tests [38].

Synthesis methods

We will synthesise evidence in accordance with Chapters 10 and 12 of the Cochrane Handbook [39, 40]. We will use Review Manager (RevMan) for data management and meta‐analyses [41].

We will tabulate key study characteristics (prevention stratum, intervention strategy components, comparator, target definition/threshold category, follow‐up, and outcome definitions) and assess eligibility for each synthesis against prespecified groups. Studies will contribute to a synthesis only when participants, interventions, comparators, and outcomes are sufficiently similar to provide a clinically meaningful pooled estimate.

As explained, the primary comparison is treat‐to‐target versus no‐target strategies. Trials that directly compare lower versus higher target thresholds (both goal‐directed) will be synthesised separately (and stratified by prevention status where data permit).

We will analyse randomised trials and non‐randomised studies of interventions separately and will not pool their results in the same meta‐analysis. For NRSIs, we will include only adjusted effect estimates in the synthesis, considering some or all of the aforementioned confounders. We will consider whether studies have adjusted for these factors, where relevant, when assessing risk of bias due to confounding and when interpreting the findings. Studies at critical risk of bias due to confounding (including those with limited or no adjustment for relevant confounders) will not be included in the synthesis.

When quantitative synthesis is appropriate, we will pool effect estimates using the random‐effects model to account for expected clinical and methodological diversity in strategy implementation across settings. We will use inverse‐variance methods; for dichotomous outcomes, we will pool risk ratios (or hazard ratios for time‐to‐event outcomes where reported), and for continuous outcomes, mean differences or standardised mean differences as appropriate. We will estimate between‐study variance (τ²) using Restricted Maximum Likelihood REML [42], and calculate 95% CIs for the summary effect using Hartung‐Knapp‐Sidik‐Jonkman methods where feasible (with a Wald‐type CI as a fallback if required for model convergence). If Peto odds ratios are used, we will use the fixed‐effect model [39].

If meta‐analysis is not appropriate (e.g. substantial heterogeneity in strategy definition/implementation, incompatible outcome definitions, or sparse data), we will summarise findings narratively following SWiM principles [43], structured by prevention stratum, comparison, and outcome domain, supported by tabulation of effect estimates and direction of effect [40].

Investigation of heterogeneity and subgroup analysis

For pairwise meta‐analyses, we will assess heterogeneity using visual inspection of forest plots, the Chi² test, and the I² statistic [44], and interpreting these measures in accordance with Chapter 10 of the Cochrane Handbook [39]. We will examine potential reasons for variability across studies, including the baseline cardiovascular risk and baseline lipid levels, comorbidities (e.g. diabetes), background care, and how outcomes were defined or measured.

Where sufficient data are available and there is a clinically plausible rationale, we will aim to conduct subgroup analyses when 10 or more studies are available for the following prespecified subgroups.

• Age (less than 40 years of age, 40 to 59, 60 to 74, more than 75)

• Sex (male versus female)

• Metabolic disorders: dysglycaemia (prediabetes/diabetes), metabolic syndrome, and familial hypercholesterolaemia

• Initiation thresholds for lipid‐lowering therapy

  • LDL or other lipid (i.e. triglycerides) or parameter (Lipoprotein A) initiation thresholds

  • Calculated 10‐year CVD risk (lab‐based or non‐lab based models) (less than 5%, 5 to 10%, 10% to 20%, 20% to 30%, more than 30%)

• Chronic kidney disease (CKD)—using study‐reported definitions where available (presence of CKD versus no CKD)

• HIV status

• Type of lipid‐lowering therapy: statins, ezetimibe, PCSK9‐targeting therapies, bempedoic acid, fibrates, bile acid sequestrants, and combination therapy

If subgroup analyses are performed, we will use the formal test for subgroup differences in RevMan [39, 41].

Sensitivity analysis

Where data permit, we will conduct sensitivity analyses in accordance with Chapter 10 of the Cochrane Handbook [39]. We will explore the robustness of findings by restricting analyses to studies at overall low risk of bias and to studies without missing outcome data. For cluster‐randomised trials requiring an externally obtained or imputed intracluster coefficient (ICC), we will repeat the analysis using plausible alternative ICC values.

Certainty of the evidence assessment

We will assess the certainty of evidence using the GRADE approach and prepare summary of findings tables in line with Chapter 14 of the Cochrane Handbook [45, 46]. We will use GRADEpro GDT to develop the tables [47]. At least two review authors will independently assess the certainty of the evidence for each prioritised outcome; disagreements will be resolved by discussion or by involving a third review author.

We will assess certainty across the five GRADE domains: risk of bias, inconsistency, indirectness, imprecision, and publication bias, and downgrade the certainty of evidence by one or two levels for serious or very serious concerns in these domains. We will rate the certainty of evidence as high, moderate, low, or very low, using standard GRADE guidance [45, 46]. If non‐randomised studies are included, we will assess and present their certainty separately, will not combine certainty assessments across study designs, and will consider potential upgrading factors where applicable (e.g. large effect).

We will prepare a summary of findings table for the primary comparison of treat‐to‐target versus no‐target lipid‐lowering strategies. The outcomes that we have prioritised for the main summary of findings table are the seven critical outcomes: all‐cause mortality, ASCVD death, 3‐point MACE, stroke or transient ischaemic attack, coronary heart disease, aortic atherosclerotic disease, and peripheral artery disease. For each outcome, we will prioritise the medium‐term follow‐up, where available; otherwise, we will use the longest available follow‐up and indicate the timeframe. For dichotomous outcomes, we will present relative effects and anticipated absolute effects.

As part of the review's supplementary materials, we will present summary of finding tables for other comparisons (lower target versus higher target and single target or no target versus multiple risk‐stratified targets) for all outcomes at medium‐ and long‐term follow‐up.

Equity considerations

Guided by the PROGRESS‐Plus framework and informed by WHO priorities for this review, we will consider whether the effects of treat‐to‐target versus no‐target lipid‐management strategies differ across equity‐relevant characteristics where data are available. In particular, we will examine evidence by factors such as age and sex, baseline cardiovascular risk and prevention status (primary versus secondary prevention/established CVD), key comorbidities (e.g. diabetes, CKD, HIV) [48]. Where subgroup analyses are not feasible due to sparse or inconsistent reporting, we will describe equity‐relevant reporting and contextual factors narratively.

Consumer involvement

We will involve consumers through consultation with the WHO guideline panel, which includes guideline users and individuals with lived experience relevant to cardiovascular disease prevention and long‐term pharmacological treatment. Involvement from any consumers will occur during the interpretation of the review findings and the preparation of the Plain Language Summary. No formal qualitative research methods are planned.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD016388.

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

Supplementary material 2 SWAR (study within a review) protocol: evaluation of AI‐assisted versus human‐only data extraction and risk of bias assessment in systematic reviews

Supplementary material 3 Thresholds for minimally important differences (MIDs)

New

Additional information

Contributions of authors

• KS drafted the protocol.

• JF contributed to and advised on the methodological and statistical approach (including planned evidence synthesis).

• BB and NSK provided senior methodological guidance.

• CMEL developed the search strategy.

• PET, SO, and AMZ reviewed the draft and provided feedback.

All authors reviewed and approved the final version of the protocol.

Declarations of interest

• Kamyar Shokraee: none declared

• Juan Franco: Senior Editor for the Cochrane Library (not involved in the editorial process for this review)

• Petek Eylul Taneri: none declared

• Siavosh Olfati: none declared

• Ana‐Mihaela Zorger: none declared

• Camila Micaela Escobar Liquitay: none declared

• Nicole Skoetz: Senior Editor for the Cochrane Library (not involved in the editorial process for this review)

• Brenda Bongaerts: Senior Editor for the Cochrane Library (not involved in the editorial process for this review)

Sources of support

Internal sources

• Institute of General Practice, Centre for Health and Society Medical Faculty, Heinrich Heine University Düsseldorf Düsseldorf, Germany

  Provides in‐kind support to JVAF and BB for the conduct of Cochrane reviews

External sources

• World Health Organization, Switzerland

  Provided funding to the review teams (Heinrich Heine University Düsseldorf and University of Cologne) to conduct this review

Registration and protocol

Cochrane approved the proposal for this review in January 2026.

Data, code and other materials

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

AI‐assisted data extraction and risk‐of‐bias assessment: Claude Sonnet (Anthropic) [27] ‐ evaluation and workflow described in the SWAR protocol in Supplementary material 2

Disclosure of artificial intelligence use

We used Grammarly (Grammarly Inc; January to February 2026) to support language editing (grammar, spelling, and style) of the protocol text. All suggested edits were reviewed and approved by the authors, who take full responsibility for the final content.

We used ChatGPT (OpenAI; 5.2/5.5; January to February 2026) to assist with drafting and refining non‐substantive text (e.g. phrasing and readability) for the protocol manuscript. All AI‐assisted text was reviewed, revised as needed, and approved by the authors, who take full responsibility for the final content and any interpretations.

The review authors plan to use AI‐assisted data extraction and risk‐of‐bias assessment: Claude Sonnet (Anthropic) [27]. The evaluation and workflow for this process is described in the SWAR protocol in Supplementary material 2.