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Altering the availability or proximity of food, alcohol, and tobacco products to change their selection and consumption.

BACKGROUND
Overconsumption of food, alcohol, and tobacco products increases the risk of non-communicable diseases. Interventions to change characteristics of physical micro-environments where people may select or consume these products - including shops, restaurants, workplaces, and schools - are of considerable public health policy and research interest. This review addresses two types of intervention within such environments: altering the availability (the range and/or amount of options) of these products, or their proximity (the distance at which they are positioned) to potential consumers.


OBJECTIVES
1. To assess the impact on selection and consumption of altering the availability or proximity of (a) food (including non-alcoholic beverages), (b) alcohol, and (c) tobacco products.2. To assess the extent to which the impact of these interventions is modified by characteristics of: i. studies, ii. interventions, and iii.


PARTICIPANTS



SEARCH METHODS
We searched CENTRAL, MEDLINE, Embase, PsycINFO, and seven other published or grey literature databases, as well as trial registries and key websites, up to 23 July 2018, followed by citation searches.


SELECTION CRITERIA
We included randomised controlled trials with between-participants (parallel group) or within-participants (cross-over) designs. Eligible studies compared effects of exposure to at least two different levels of availability of a product or its proximity, and included a measure of selection or consumption of the manipulated product.


DATA COLLECTION AND ANALYSIS
We used a novel semi-automated screening workflow and applied standard Cochrane methods to select eligible studies, collect data, and assess risk of bias. In separate analyses for availability interventions and proximity interventions, we combined results using random-effects meta-analysis and meta-regression models to estimate summary effect sizes (as standardised mean differences (SMDs)) and to investigate associations between summary effect sizes and selected study, intervention, or participant characteristics. We rated the certainty of evidence for each outcome using GRADE.


MAIN RESULTS
We included 24 studies, with the majority (20/24) giving concerns about risk of bias. All of the included studies investigated food products; none investigated alcohol or tobacco. The majority were conducted in laboratory settings (14/24), with adult participants (17/24), and used between-participants designs (19/24). All studies were conducted in high-income countries, predominantly in the USA (14/24).Six studies investigated availability interventions, of which two changed the absolute number of different options available, and four altered the relative proportion of less-healthy (to healthier) options. Most studies (4/6) manipulated snack foods or drinks. For selection outcomes, meta-analysis of three comparisons from three studies (n = 154) found that exposure to fewer options resulted in a large reduction in selection of the targeted food(s): SMD -1.13 (95% confidence interval (CI) -1.90 to -0.37) (low certainty evidence). For consumption outcomes, meta-analysis of three comparisons from two studies (n = 150) found that exposure to fewer options resulted in a moderate reduction in consumption of those foods, but with considerable uncertainty: SMD -0.55 (95% CI -1.27 to 0.18) (low certainty evidence).Eighteen studies investigated proximity interventions. Most (14/18) changed the distance at which a snack food or drink was placed from the participants, whilst four studies changed the order of meal components encountered along a line. For selection outcomes, only one study with one comparison (n = 41) was identified, which found that food placed farther away resulted in a moderate reduction in its selection: SMD -0.65 (95% CI -1.29 to -0.01) (very low certainty evidence). For consumption outcomes, meta-analysis of 15 comparisons from 12 studies (n = 1098) found that exposure to food placed farther away resulted in a moderate reduction in its consumption: SMD -0.60 (95% CI -0.84 to -0.36) (low certainty evidence). Meta-regression analyses indicated that this effect was greater: the farther away the product was placed; when only the targeted product(s) was available; when participants were of low deprivation status; and when the study was at high risk of bias.


AUTHORS' CONCLUSIONS
The current evidence suggests that changing the number of available food options or altering the positioning of foods could contribute to meaningful changes in behaviour, justifying policy actions to promote such changes within food environments. However, the certainty of this evidence as assessed by GRADE is low or very low. To enable more certain and generalisable conclusions about these potentially important effects, further research is warranted in real-world settings, intervening across a wider range of foods - as well as alcohol and tobacco products - and over sustained time periods.


Data collection and analysis
We used a novel semi-automated screening workflow and applied standard Cochrane methods to select eligible studies, collect data, and assess risk of bias. In separate analyses for availability interventions and proximity interventions, we combined results using randomeffects meta-analysis and meta-regression models to estimate summary effect sizes (as standardised mean differences (SMDs)) and to investigate associations between summary effect sizes and selected study, intervention, or participant characteristics. We rated the certainty of evidence for each outcome using GRADE.

Main results
We included 24 studies, with the majority (20/24) giving concerns about risk of bias. All of the included studies investigated food products; none investigated alcohol or tobacco. The majority were conducted in laboratory settings (14/24), with adult participants (17/24), and used between-participants designs (19/24). All studies were conducted in high-income countries, predominantly in the USA (14/24).
Six studies investigated availability interventions, of which two changed the absolute number of different options available, and four altered the relative proportion of less-healthy (to healthier) options. Most studies (4/6) manipulated snack foods or drinks. For selection outcomes, meta-analysis of three comparisons from three studies (n = 154) found that exposure to fewer options resulted in a large reduction in selection of the targeted food(s): SMD −1.13 (95% confidence interval (CI) −1.90 to −0.37) (low certainty evidence). For consumption outcomes, meta-analysis of three comparisons from two studies (n = 150) found that exposure to fewer options resulted in a moderate reduction in consumption of those foods, but with considerable uncertainty: SMD −0.55 (95% CI −1.27 to 0.18) (low certainty evidence).
Eighteen studies investigated proximity interventions. Most (14/18) changed the distance at which a snack food or drink was placed from the participants, whilst four studies changed the order of meal components encountered along a line. For selection outcomes, only one study with one comparison (n = 41) was identified, which found that food placed farther away resulted in a moderate reduction in its selection: SMD −0.65 (95% CI −1.29 to −0.01) (very low certainty evidence). For consumption outcomes, meta-analysis of 15 comparisons from 12 studies (n = 1098) found that exposure to food placed farther away resulted in a moderate reduction in its consumption: SMD −0.60 (95% CI −0.84 to −0.36) (low certainty evidence). Meta-regression analyses indicated that this effect was greater: the farther away the product was placed; when only the targeted product(s) was available; when participants were of low deprivation status; and when the study was at high risk of bias.

Authors' conclusions
The current evidence suggests that changing the number of available food options or altering the positioning of foods could contribute to meaningful changes in behaviour, justifying policy actions to promote such changes within food environments. However, the certainty of this evidence as assessed by GRADE is low or very low. To enable more certain and generalisable conclusions about these potentially important effects, further research is warranted in real-world settings, intervening across a wider range of foods -as well as alcohol and tobacco products -and over sustained time periods.

B A C K G R O U N D Description of the condition
Non-communicable diseases, principally cardiovascular diseases, diabetes, certain forms of cancer, and chronic respiratory diseases, accounted for an estimated 68% of all deaths worldwide in 2012 (WHO 2016). Major risk factors for non-communicable diseases include metabolic and dietary risk factors linked to food consumption (e.g. high body mass index, high systolic blood pressure), as well as smoking and alcohol use -risks that are, in principle, modifiable. These are also amongst the most significant risk factors for total disease burden, both globally and in high-income countries specifically (GBD 2018). Identifying interventions that are effective in achieving sustained health behaviour change across populations and countries is therefore one of the most important public health challenges of the 21st century.

Description of the intervention
It is increasingly recognised that the physical environments that surround us can exert considerable influences on our health-related behaviours and that altering these environments may provide a catalyst for behaviour change (Cohen 2016; Marteau 2012; Stok 2017). We have previously described a set of interventions that involve altering small-scale physical environments -or micro-environments -with the intention of changing health-related behaviours (Hollands 2013a; Hollands 2017a), which have also been described as 'choice architecture' (or 'nudge') interventions (Cadario in press; Szaszi 2018; Thaler 2008). These interventions involve changing characteristics of, or cues within, environments where people may select or consume food, alcohol, or tobacco including restaurants, workplaces, schools, homes, bars, pubs, supermarkets, or shops. They have received increased policy and research interest in recent years as a result of several factors (Marteau 2015), including shifts in theoretical understanding, supportive empirical evidence, political acceptability (with governments preferring 'light-touch' rather than legislative or regulatory approaches), and public acceptability (with evidence suggesting these types of interventions are relatively acceptable) (Petrescu 2016; Reisch 2016; Reynolds 2019). Perceived feasibility and low cost, whereby such interventions may be viewed as easily implemented at scale without complex legislative or regulatory processes or the need for individual delivery, may also contribute. The placement of food, alcohol, and tobacco products within the physical environment can influence their selection and consumption. Within the Typology of Interventions in Proximal Physical Micro-Environments (TIPPME) intervention typology (Hollands 2017a), a framework developed for characterising interventions in physical micro-environments, 'placement' interventions comprise two key, more specific intervention types: first, interventions that target the 'availability' of food, alcohol, or tobacco products within a specific environment -essentially, what is made available for selection or consumption, or both; and second, interventions focused on how available products are positioned within a specific environment. Our specific focus with respect to how products are positioned is on the 'proximity' of food, alcohol, or tobacco products to and from people, which can be altered by moving the products nearer or farther away to make them more or less accessible. Availability and proximity interventions are described further below.

Interventions that alter availability
These interventions involve manipulating the available food, alcohol, or tobacco product options in an environment such as a shop, bar, or restaurant. This can be achieved by providing, either: a) a greater or lesser range of different product options (within a targeted range or category), for example: • food -providing a wider range of healthier meal options, or a reduced number of less-healthy meal options in a restaurant or cafeteria; or a reduced range of snacks in vending machines; • alcohol -providing a wider range of different low-alcohol options in a bar or pub; or a reduced range of types of wine or beer in a restaurant; and • tobacco -providing a reduced range of types of tobacco product in a shop. b) a greater or lesser amount (number) of discrete units of a product. In this case, the range of different product options might not be changed, but the number of available units of the existing product options is manipulated. For example: • food -making a lesser amount of (a range of ) chocolate bars on display in a supermarket; • alcohol -making a greater amount of (a range of ) lowalcohol beer bottles available in a bar or pub; and • tobacco -making a lesser amount of (a range of ) cigarettes available in a shop. c) a combination of a) and b). These possible manipulations can concern changes in the absolute number of different options available, or changes in relative proportions, such as the relative number (proportion) of less-healthy (to healthier) options that are available.

Interventions that alter proximity
These interventions concern the positioning of products that are available within that environment. The term we have used -'proximity' -reflects the fact that the predominant intervention of this type within the current context involves moving food, alcohol, or tobacco products closer to or farther away from people, such as placing a healthier product such as fruit in a more proximal (and therefore convenient) position within a shop to encourage its purchase (Kroese 2016). By reducing or increasing the distance to be traversed or reached, such interventions can alter the degree of convenience, and of effort required for potential consumers to select or consume these products. The proximity of a product (how close or far away it is) is altered in relation to key physical features in environments, such as typical or expected walking routes, building entrances, checkouts in supermarkets or shops, or seating. Examples include positioning a display of food products close to a shop's entrance (e.g. 1 m), aiming to enable convenient selection of the products, versus this being located at a distance that requires customers to walk a greater distance to engage with the display (e.g. 20 m). Alternatively, it could involve altering the positioning of a food product to be within arm's reach of a potential consumer (e.g. placed 20 cm from seating) versus requiring them to leave their seating and walk to take the food product (e.g. placed 2 m from seating). A detailed conceptual framework for these interventions has been developed (Pechey under review).

How the intervention might work
There are considerable influences on behaviour that are beyond individuals' deliberative control. Indeed, it has been suggested that much human behaviour occurs outside of awareness, cued by stimuli in environments and resulting in actions that may be largely unaccompanied by conscious reflection (Marteau 2012;Neal 2006). This proposition has led to increasing policy and research attention being placed on interventions with mechanisms of action that may be less dependent on the conscious engagement of the recipients (Hollands 2016), including interventions that involve altering the placement of objects within the physical environments that surround and cue behaviour. Various underlying mechanisms of action have been proposed for both availability and proximity interventions (Pechey under review), although it is difficult to assess these outside of artificial, controlled environments. In relation to availability, whether options are available (or absent) within a given environment inevitably shapes and constrains people's possible responses. The more product options that are available, the more likely it is that an actor will encounter an option they are willing to select or consume (Chernev 2011). Exposure may also increase the salience of, and the attention directed towards, products and elicit a 'mereexposure' effect -whereby repeated exposure to a product can elicit increased liking (Dalenberg 2014). Altering a range of available products could also have the effect of implying a new social norm about which types of products are acceptable or commonplace, and this could influence selection and consumption. Whilst currently largely unexplored, the sum of these potential mechanisms is that increasing the range of options for a given product or category should increase its selection or consumption, albeit subject to people engaging with the product in the first place. This will be influenced by many factors, including characteristics of the person (such as hunger) and of the product (such as its attractiveness or palatability). In addition, it has been suggested that if the range of available products is increased, choosing between these options becomes more reliant on a reasoning process, meaning that people may make different choices based on what they are most able to justify (Sela 2009). Furthermore, if the range of available product options remains the same, but the number of units of these products increases, this may increase their visibility or salience and therefore encourage selection or consumption. In relation to proximity, the central role of physical and mental effort has been highlighted ( Bar-Hillel 2015). Humans tend to take the least effortful course of action without the need for conscious deliberation, and so physical environments can shape responses by capitalising on this phenomenon. Consequently, products placed nearer an actor require less effort to obtain than those placed farther away, and this may correspondingly impact on motivation to select or consume them (Hunter 2018). Other than the effort needed (or perceived as such), more distal products may also be less visible and less salient (Maas 2012). Increasing physical distance may also increase 'psychological distance' -the subjective experience of distance from the self in that time and place -and so more distal products may be focused upon in a less detailed way or be subject to more deliberation or rationalisation, which may impact one's behaviour (Trope 2010).

Why it is important to do this review
A systematic scoping review of evidence for the effects of physical micro-environment interventions identified a substantial number of studies that have investigated the effects of altering the availability and proximity of products on health-related behaviours (Hollands 2013b). The majority of these studies focused on food products, where interventions have significant potential given the necessity of consumption of these products and their ubiquity within many environments. However, because both tobacco and alcohol use also involve the selection and consumption of products, such interventions may also have the potential to change these behaviours via similar mechanisms. We have synthesised evidence for the effects of availability and proximity interventions within a single systematic review because we conceptualise them both as interventions that alter the placement of products within physical micro-environments. To our knowledge, evidence from these studies has yet to be synthesised using rigorous systematic review methods that include quantitative synthesis, assessment of risk of bias, and investigation of potential effect modifiers, or to encompass alcohol and tobacco use, although parts of this evidence base have been reviewed. As such, we do not yet have reliable estimates of the effects of these types of interventions on product selection and consumption, nor of the influence of factors that may modify any such effects. Both are necessary to inform the selection and design of effective public health interventions, particularly given increasing research and policy interest in interventions that alter the physical environment to make unhealthier behaviours less likely and healthier behaviours more likely. This interest is evidenced by the substantial public and policy interest in a previous Cochrane Review on portion, package, and tableware size (Hollands 2015), which has influenced policy debate in the UK and Australia (Jones 2016). Poor diet, harmful alcohol use, and smoking are socially patterned, being more common amongst those in lower socioeconomic positions, thereby contributing to the increased morbidity and premature mortality observed in these groups (Stringhini 2010). Behaviour change interventions that focus on the provision of educational information to individuals and encouragement for them to make active choices, potentially widen health inequalities (Lorenc 2013;McGill 2015). Interventions that instead aim to alter the environments that people are exposed to and therefore may be less reliant on conscious, reflective engagement (Hollands 2016), could have a greater potential to reduce, or at least not increase, health inequalities. It has been suggested that this may be because they rely less on recipients' cognitive resources including levels of literacy, numeracy, and cognitive control, which on average are lower in population subgroups experiencing higher levels of social and material deprivation (Hall 2014). The current review sought to identify evidence for differential effects of exposure to these interventions between socioeconomic groups. To our knowledge, no studies of the effects of these interventions have been conducted in low-and middle-income countries (LMICs) that would enable a comparison of effects between studies in high-income countries (HICs) and LMICs, but we sought to identify such evidence. Purposively considering socioeconomic status and country context factors in our analysis (and highlighting gaps in the evidence base) enabled the opportunity to assess the potential impact such interventions could have upon health inequalities.

O B J E C T I V E S
1. To assess the impact on selection and consumption of altering the availability or proximity of (a) food (including non-alcoholic beverages), (b) alcohol, and (c) tobacco products.
2. To assess the extent to which the impact of these interventions is modified by characteristics of: i. studies, ii. interventions, and iii. participants.

Types of studies
Randomised controlled trials (RCTs) or cluster-RCTs with between-participants (parallel group) or within-participants (crossover) designs, conducted in laboratory or field ('real-world') settings. We excluded non-randomised studies because, first, a scoping review indicated that a sufficient number of eligible randomised studies were likely available to enable quantitative synthesis of evidence for intervention effects (Hollands 2013a). Second, compared with RCTs, non-randomised studies rely on more stringent and sometimes non-verifiable assumptions in order to confer confidence that the risk of systematic differences between comparison groups beyond the intervention of interest (i.e. confounding) is sufficiently low to permit valid inferences about causal effects. If randomised assignment was not clear in studies otherwise considered eligible for inclusion at the full-text assessment stage, we only included the study if study authors had confirmed that randomisation occurred. We also excluded randomised studies that had only a single participating site in the intervention or the comparator group, or both, because this would result in the treatment effect being completely confounded with the site characteristics.

Types of participants
Adults and children exposed to the interventions. We defined adults as those 18 years of age or over, and children as those under 18 years (United Nations 1989). We excluded studies where the product was selected and fed directly by one person to another (e.g. mother-child dyads). No other exclusion criteria in relation to demographic, socioeconomic, or clinical characteristics were set. We excluded studies involving non-human participants (i.e. animal studies).

Types of interventions
Eligible interventions were those that involved altering the availability or proximity of food (including non-alcoholic beverages), alcohol, or tobacco products within 'physical micro-environments', defined here as small-scale physical environments where people gather for specific purposes and activities, such as restaurants, workplaces, schools, homes, bars, pubs, supermarkets, or shops (Hollands 2017a; Swinburn 1999). Availability interventions and proximity interventions are defined in the Description of the intervention section, and details of specific eligibility criteria for each intervention type are provided below.

Availability interventions
'Availability interventions' eligible for consideration in this review were those that involved comparing the effects of exposure to at least two differing (i.e. higher versus lower) levels of availability of a manipulated food, alcohol, or tobacco product. This allowed us to examine whether, for example, making a food product more available increases its consumption, or making a food product less available decreases its consumption. The 'product' can be operationalised as applying to types of a specific product (e.g. fruit, chocolate bars) or to broader ranges or categories of products (e.g. energy-dense snack foods; low-fat meals). For alcohol and tobacco products, we also considered including interventions in which the availability of specific recognised alternatives to those products that are not themselves alcohol and tobacco products is manipulated within alcohol or tobacco selection and consumption contexts (e.g. alcohol-free variants in the case of alcohol, or e-cigarettes in the case of tobacco).

Additional inclusion criteria
1. The comparison of different levels of availability must be explicitly described, as opposed to this being inferred by the review team. For example, a review author could infer that a supermarket sales promotion would increase the number of products on display in store, but a study would only be included if this was clearly stated by the authors.
2. We included multicomponent interventions in which there were concurrent intervention components that were unrelated to availability, providing those additional components were implemented wholly within the same physical microenvironment as in the availability intervention, involving changes to the product itself or its proximal physical environment. Examples include nutritional labelling on the product itself, or promotional signage placed near to the product. We planned to treat confounded and unconfounded components differently (see Data synthesis). We excluded the following interventions.
1. Multicomponent interventions in which there were concurrent intervention components that were unrelated to availability, where those additional components were not implemented wholly within the same micro-environment as in the availability intervention, involving changes to the product itself or its proximal physical environment. Examples of such ineligible intervention components include health education programmes or marketing campaigns.
2. Interventions in which availability may be altered indirectly as a result of a higher-level intervention but is not directly and systematically altered (e.g. organisational-level interventions to encourage the wider availability of healthier products within a workplace or set of workplaces, or national-or regional-level policy interventions to encourage schools to modify their environments). Whilst availability may be changed as a result of the higher-level intervention, this is not directly manipulated to safeguard implementation fidelity.
3. Interventions within analogue studies that do not manipulate real food, alcohol, or tobacco products but instead may use written vignettes, computer or questionnaire tasks, or mock products to assess the impact of altering availability. 4. Interventions in which the range of product options is unchanged (as regards being perceptible prior to selection) in terms of the different types or categories of products that are available, but changes are made in the range of ways in which those same products are formulated (as regards being perceptible prior to selection) or presented, such as flavour, colour, size, or shape.
5. Interventions in which the environmental contexts or opportunities for selection and consumption are not comparable between intervention and control groups. We therefore excluded interventions that involved removing (or adding) the entire range of food, alcohol, or tobacco products within a given microenvironment (e.g. studies examining the effectiveness within a specified environment of complete smoking or alcohol bans), as well as those that involved substantial changes to its infrastructure (such as building new shops or restaurants) or its furniture (e.g. adding or removing fixtures and fittings). We also excluded interventions in which availability differed between intervention and control arms due to: additional exposure to foods via assigned dietary programmes (e.g. prescribed diets); education (e.g. taste-testing sessions, cooking lessons, or food education); or other means of prescribed distribution of products to participants.
6. Interventions in which the availability of a product was not altered in terms of its range or amount but as a result of temporal (e.g. changing hours of sale or altering a range of available products over time) or spatial (e.g. changing the places in which a product can be selected or consumed) factors (Han 2014; Sherk 2018).

Proximity interventions
'Proximity interventions' eligible for consideration in this review were those that involved comparing the effects of exposure to at least two differing (i.e. higher versus lower) levels of proximity of a manipulated food, alcohol, or tobacco product. Whilst there may be other ways of altering the positioning of products that do not impact on their proximity, we have purposefully limited our scope to proximity interventions. This is because any other such studies would be difficult to assess within the same framework specified for use in the current review, which focuses on the effects of altering the quantity or degree (i.e. increase versus decrease) of a specific property (i.e. proximity).

Additional inclusion criteria
1. The comparison of different levels of proximity had to be explicitly described, as opposed to this being inferred by the review team. For example, a review author could infer that a redesigned layout of a cafeteria or restaurant might increase or decrease proximity from a given point of reference, but a study would only be included if this change in proximity was clearly stated by authors.
2. As per availability interventions, we included multicomponent interventions in which there were concurrent intervention components that were unrelated to proximity, providing those additional components were implemented wholly within the same physical micro-environment as in the proximity intervention, involving changes to the product itself or its proximal physical environment. Examples include nutritional labelling on the product itself, or promotional signage placed near to the product. We excluded the following interventions.
1. As per availability interventions, multicomponent interventions in which there were concurrent intervention components that were unrelated to proximity, where those additional components were not implemented wholly within the same micro-environment as in the proximity intervention, involving changes to the product itself or its proximal physical environment.
2. Interventions in which proximity may be altered indirectly as a result of a higher-level intervention but was not directly and systematically altered (e.g. organisational-level interventions to encourage the redesign of the layout of school or workplace cafeterias). Whilst proximity may be changed as a result of the higher-level intervention, this is not directly manipulated to safeguard implementation fidelity.
3. Interventions within analogue studies that do not manipulate real food, alcohol, or tobacco products but instead may use written vignettes, computer or questionnaire tasks, or mock products to assess the impact of altering proximity. 4. Interventions in which the proximity of text, symbols, or images that relate to products is altered (e.g. on a sign, advertisement, poster, menu, leaflet, or computer screen (e.g. online supermarket)), but the proximity of the actual products to be selected or consumed is not. 5. Interventions in which the environmental contexts or opportunities for selection and consumption are not comparable between intervention and control groups. We therefore excluded interventions that involved substantial changes to the infrastructure of the environment or its furniture. Studies including both availability and proximity intervention components were eligible for inclusion in the review.

Types of outcome measures
Eligible studies had to incorporate one or more objective measures of unconstrained selection (with or without purchasing) or consumption of the manipulated food, alcohol, or tobacco product(s). For example, a study investigating the effects of increasing the availability or proximity of fruit within a shop on healthier purchasing could include a specific measure of fruit (i.e. the manipulated product) selected only, or a broader measure at category level that encompasses both fruit selection and selection of nonfruit options available in the shop (e.g. a measure of selection of all healthier food options). Either would represent an appropriate primary outcome. Studies may additionally include measures that relate specifically to non-manipulated products -in the given example there may also be a measure of selection of non-fruit op-tions only. Such measures would represent appropriate secondary outcomes. Objective measurement may involve sales data or calculating the amount of a product consumed by subtracting the amount remaining after consumption from the total amount presented to the participant. Alternatively, it may involve direct observation of selection or consumption behaviour by outcome assessors. Subjective measurement would involve participant self-report. By unconstrained, we refer to behaviour of participants that is not constrained or regulated by either explicit instructions or some other action of the researcher. For example, we excluded studies that manipulated the availability of foods that are not selected, plated, or served under the direction of the participant, but where foods were presented to them individually with the instruction to select or consume. Quantities selected or consumed may have been measured over a time period less than or equal to one day (immediate) or exceeding one day (longer term). Our choice of eligible outcome constructs reflects a focus on the assessment of the effects of eligible interventions in terms of the types and amounts of food, alcohol, and tobacco people consume, coupled with recognition that the amount selected (with or without purchasing) is an important intermediate endpoint in pathways to consumption.

Primary outcomes
Measures of unconstrained selection (with or without purchasing) or consumption of the manipulated food, alcohol, or tobacco product(s). We anticipated encountering a range of measures of these outcome constructs amongst included studies, and present the following examples of likely measures below. 1. Selection of a product (a) without purchase, or b) with purchase. Assessment of the amounts of products (e.g. food, drink, alcohol, or tobacco products), energy or substances (e.g. saturated fat, alcohol, carbon monoxide) selected, measured in applicable natural units (e.g. kilojoules, grams). Depending on the study setting, a product may be selected with or without this involving a purchase, that is a transfer of money to the vendor. In cases where there is no purchasing, selection may be comparable to typical purchasing (e.g. products being selected in a restaurant or bar where there is no charge for them) or it may be behaviour that necessarily precedes consumption in that context, such as serving an amount of a food product onto a plate or pouring an amount of drink into a glass. 2. Consumption (intake) of a product. As per selection, assessment of the amounts of products (e.g. food, drink, alcohol, or tobacco products), energy, or substances (e.g. saturated fat, alcohol, carbon monoxide) consumed, measured in applicable natural units (e.g. kilojoules, grams).
As with the specified primary outcomes, secondary outcomes are also measures of unconstrained selection (with or without purchasing) or consumption of food, alcohol, or tobacco products. However, secondary outcomes apply to other products that are available in the same micro-environment at the same point of selection or consumption as the manipulated product(s), but that are not themselves manipulated as regards to their availability or proximity. Due to the nature of the interventions, we anticipated that adverse effects (other than unwanted health-harming effects on selection or consumption, which would be captured by the specified primary and secondary outcomes) were unlikely to occur, be assessed or reported. However, any adverse events or harms reported in the included studies were noted.

Conceptual model
To supplement study eligibility criteria, we developed a provisional conceptual model that was published in the protocol for this review (Hollands 2017b). The conceptual model was design-oriented in the sense that it was intended to help direct the review process by providing a simplified visual representation of the causal system of interest (Anderson 2011), that is the proposed causal pathway between eligible interventions and their outcomes (behavioural endpoints), and potential moderators of that relationship (effect modifiers) given that differential effects are plausible (Anderson 2013). We used the provisional conceptual model to inform the development of search strategies, data extraction forms, and a provisional framework for the statistical analysis of the data collected from the eligible studies (see Search methods for identification of studies and Data collection and analysis). We revised the conceptual model iteratively, as we encountered evidence from eligible studies during the course of the review process, and documented revisions. We used the iterations of the conceptual model as a reference point for the design (in the protocol), conduct, and reporting (postprotocol) of the systematic review (Anderson 2013). In practice, iterative refinement of the conceptual model involved incorporating further potential effect modifiers identified during the data collection process, which were then considered in the analysis and reporting of these data. The final version of the conceptual model is shown in Figure 1, with details of its development in Data collection and analysis.

Electronic searches
We developed a MEDLINE search strategy by combining sets of controlled vocabulary and free-text search terms based on the eligibility criteria described above (see Criteria for considering studies for this review). It was developed with the intention of being highly sensitive (at the expense of precision) to give confidence in its ability to detect potentially eligible title and abstract records. This search strategy was externally peer-reviewed by an information retrieval specialist and co-convenor of the Cochrane Information Retrieval Methods Group and revised based on their peer-review comments. We tested and calibrated the MEDLINE search strategy for its sensitivity to retrieve a reference set of 24 records of reports of potentially eligible studies that were identified within a preceding, broader scoping review of interventions within physical micro-environments (Hollands 2013a

Searching other resources
We conducted electronic searches of the following grey literature databases using search strategies adapted from the final MEDLINE search strategy, as described above: • Conference Proceedings Citation Index -Science (Web of Science) (1990 to 24th July 2018); • Conference Proceedings Citation Index -Social Science & Humanities (Web of Science) (1990 to 24th July 2018); and • OpenGrey (1997 to 24th July 2018).
We searched trial registers (US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov ( www.clinicaltrials.gov/), the World Health Organization International Clinical Trials Registry Platform ( apps.who.int/trialsearch/), and the EU Clinical Trials Register ( www.clinicaltrialsregister.eu/)) to identify registered trials (up to 25th July 2018), and the websites of key organisations in the area of health and nutrition, including the following: • UK Department of Health; • Centers for Disease Control and Prevention (CDC), USA; • World Health Organization (WHO); • International Obesity Task Force; and • EU Platform for Action on Diet, Physical Activity and Health.
In addition, we searched the reference lists of all eligible study reports and undertook forward citation tracking (using Google Scholar) to identify further eligible studies or study reports (up to 25th July 2018). When we found non-English language articles, we used Google Translate in the first instance to determine potential eligibility. We intended that if an article appeared to be eligible, we would have the article translated by a native language speaker or professional translation service, however no articles needed translating.

Data collection and analysis
Selection of studies Title and abstract records retrieved by the electronic searches were imported into EPPI Reviewer 4 (ER4) systematic review software (Thomas 2010). Duplicate records were identified, reviewed manually, and removed using ER4's automatic de-duplication feature. In relation to the electronic searches, search terms based on relevant intervention and comparator concepts (e.g. availab$, increas$, add$, introduc$, close$, near$, far$) are unlikely to be specific to title-abstract records of eligible studies (even when configured in multistrand search strategies), and are also likely to feature frequently in irrelevant title-abstract records. This is likely to result in large numbers of records being retrieved by electronic searches, which need to have sufficient sensitivity to capture all eligible studies. To address this challenge, we developed a semi-automated screening workflow to manage the title-abstract screening stage, deployed in ER4, which uses machine learning to assign title-abstract records for duplicate manual screening (O'Mara-Eves 2015). This workflow was designed to maximise recall of eligible studies while reducing screening workload to match the available resource, which we expected to allow for duplicate manual screening of up to a maximum of one-third of retrieved records (the 'overall screening budget'). Further details of the semi-automated screening workflow are provided in Appendix 2.
Two review authors independently undertook duplicate screening of title and abstract records retrieved by the electronic searches. We coded title and abstract records as 'provisionally eligible', 'excluded', or 'duplicate' by applying the eligibility criteria described above (see Criteria for considering studies for this review). Any disagreements in the coding of title and abstract records were identified and resolved by discussion to reach a consensus between the two review authors. When they were unable to reach a consensus, a third review author acted as an arbiter. We obtained full-text copies of corresponding study reports for all records coded as 'provisionally eligible' at the title and abstract screening stage. Two review authors independently undertook duplicate screening of full-text study reports, coding them as 'eligible' or 'excluded' by applying the eligibility criteria described above (see Criteria for considering studies for this review), with reasons for exclusion recorded. Any disagreements in the coding of fulltext study reports or reasons for exclusion were identified and resolved by discussion to reach consensus between the two review authors. In the event that any coding disagreements could not be resolved, a third review author acted as an arbiter. Bibliographic details of study reports excluded at the full-text screening stage are provided, along with the primary reason for exclusion, in the Characteristics of excluded studies table. If we identified multiple full-text reports of the same study, we linked and treated them as a single study. Some full-text reports comprising multiple eligible studies were identified, and each study was treated separately. We documented the flow of records and studies through the systematic review process and have reported this using a PRISMA flow diagram (Moher 2009).

Data extraction and management
An electronic data extraction form was developed based on the Cochrane Public Health template and the form used in a previous Cochrane Review (Hollands 2015), modified to allow extraction of all data required for this review. An initial draft of this form was piloted using a selection of included studies, to ensure that it enabled reliable and accurate extraction of appropriate data, and was amended in consultation with the review team. One review author extracted data pertaining to the characteristics of included studies. Two review authors independently extracted outcome data in duplicate. When a study with more than two intervention arms was included, only outcome data pertaining to the intervention and comparison groups that met the eligibility criteria described above were included in the review, but the Characteristics of included studies table includes details of all intervention and comparison groups present in the study. Any discrepancies in extracted outcome data were identified and resolved by checking against the study report, and by discussion and consensus, with a third review author acting as an arbiter if necessary. We contacted study authors for key unpublished data that were missing from reports of included studies.
We collected the data summarised below, comprising 28 constructs. The 26 constructs in plain type represent the maximum core dataset that at the outset we anticipated would be required based on our study eligibility criteria and the design-oriented conceptual model. It was intended that this dataset would evolve as necessary through the review process, corresponding with revisions made to the conceptual model (see Types of outcome measures), resulting in the inclusion of two additional study characteristics in italicised text. These concerned basic subtype categorisations of availability and proximity interventions, reflecting that in the review protocol, Hollands 2017b, we had presented possible subtype categorisations that would be subject to iteration or confirmation as a result of the review process. Such categorisations may be subject to further elaboration in future as the empirical or theoretical basis develops (Pechey under review). 7. Biological state (e.g. hunger) These participant characteristics cover several categories of social differentiation relevant to health equity. Collecting study-level data on these participant characteristics enabled the potential to draw inferences within our analysis concerning any differential effects of the intervention on health equity (Welch 2012). For example, proxy measures of socioeconomic status function as participant characteristics that may moderate the observed effects of the intervention on product selection and consumption. In addition, to complement investigations based on participant characteristics, we constructed a binary study-level covariate of 'socioeconomic status context' based on authors' explicit descriptions of the study sample and/or setting (see 'Study characteristics' above) that served as a proxy for the overall study context in terms of baseline levels of social and material deprivation amongst study participants. Analysis of this study-level covariate as a potential effect modifier enabled the potential to investigate specifically whether eligible interventions were more or less effective in a study context characterised by high versus low levels of social and material deprivation.

Outcome data
We anticipated that some eligible primary studies would include more than one eligible measure of selection or consumption. We used the measure of selection or consumption that mapped most closely onto the focus of the intervention, for example where only fruit products were manipulated, we used a measure that related specifically to fruit selection or consumption only. Where multiple products were manipulated concurrently, we used a measure that either related specifically to one of those products (if it was discernible that that product was the primary intervention focus), or captured selection or consumption of all manipulated products. If a study included only a category-level measure that captured selection or consumption of a wider set of products beyond those that have been manipulated (but including the manipulated product), this still represented an eligible outcome for the purposes of this review providing it could be meaningfully interpreted at category level, but was considered less desirable because it required assumptions to be made about the direction of effect in relation to the manipulated product itself. Following the application of these criteria, if there remained multiple eligible outcome measures, we selected the single measure of selection or consumption that had been (pre)specified by the study authors as the primary outcome. If no primary outcome had been specified by study authors, we selected the measure of selection or consumption most proximal to health outcomes in the context of the specific intervention. For example, if a study reported measures of both energy intake and the amount of food eaten (in grams), we selected energy intake as the measure most proximal to diet-related health outcomes, and where measures were reported relating to both intake of a healthier (e.g. low energy density) product and intake of a less-healthy (e.g. high energy density) product, we prioritised the latter. For all outcome data, we collected information on: outcome variable type (dichotomous, continuous); outcome variable definition; unit of measurement (if relevant); timing of measurement (immediate (≤ 1 day) or longer term (> 1 day)); and type of measure (objective, self-report). For dichotomous outcomes, we extracted event rates in each comparison group. For continuous outcomes, we extracted mean differences, or mean changes in final measurements from baseline measurements, for each comparison group with associated standard deviations (or if standard deviations were missing, standard errors, 95% confidence intervals or relevant tstatistics, F-statistics, or P values). For included studies using factorial designs to investigate the effects of multiple experimental manipulations, we combined groups to capture the main effects of each relevant randomised comparison.

Assessment of risk of bias in included studies
We assessed risk of bias in the included studies using the revised Cochrane 'Risk of bias' tool for randomised trials (RoB 2.0) (Higgins 2016a), employing the additional guidance for clusterrandomised and cross-over trials (Eldridge 2016; Higgins 2016b). RoB 2.0 addresses five specific domains: (1) bias arising from the randomisation process; (2) bias due to deviations from intended interventions; (3) bias due to missing outcome data; (4) bias in measurement of the outcome; and (5) bias in selection of the reported result. Two review authors independently applied the tool to each included study, and recorded supporting information and justifications for judgements of risk of bias for each domain (low; high; some concerns). Any discrepancies in judgements of risk of bias or justifications for judgements were resolved by discussion to reach consensus between the two review authors, with a third review author acting as an arbiter if necessary. Following guidance given for RoB 2.0 (Section 1.3.4) (Higgins 2016a), we derived an overall summary 'Risk of bias' judgement (low; some concerns; high) for each specific outcome, whereby the overall RoB for each study was determined by the highest RoB level in any of the domains that were assessed.

Measures of treatment effect
For continuous outcomes, we calculated the standardised mean difference (SMD) with 95% confidence intervals (CIs) to express the size of the intervention effect in each study relative to the variability observed in that study. For dichotomous outcomes, we calculated the odds ratio (OR) for each included study to express the size of the relative intervention effect between comparison groups, with the uncertainty in each result being expressed by the CI. We then re-expressed the OR as an SMD by applying the formula described in Section 9.4.6 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011). We calculated SMDs and sampling variances using means, standard deviations (SDs), and sample sizes and the corresponding equations for continuous and dichotomous data. We extracted means and SDs from published figures if they had not been reported numerically. If SDs were not reported or available from authors, they were obtained using the first appropriate rule from the following: (a) by direct calculation from statistics such as standard errors or CIs, if available; (b) by imputation, by assuming that the ratio of SD to mean for the outcome is equal to the ratio of SD to mean calculated using raw data available for other outcomes in the same study; (c) by imputation, by assuming that the ratio of SD to mean is equal to the ratio of SD to mean observed in other similar studies that reported both means and SDs.

Unit of analysis issues
In the case of cluster-randomised trials, where an analysis was reported that accounted for the clustered study design, we estimated the effect on this basis, using reported test statistics (t-statistics, Fstatistics or P values) to calculate standard errors. When this was not possible and the information was not available from the authors, we carried out an 'approximately correct' analysis according to current guidelines in Section 16.3 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We imputed estimates of the intracluster correlation (ICC) using estimates derived from similar studies or by using general recommendations from empirical research. In cases where it was not possible to implement these procedures, we gave the effect estimate as presented but have reported the unit of analysis error. For included studies with a within-participants design, we aimed to account for the design by calculating the SMD for continuous outcomes using the methods described in Section 16.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), where standard errors for outcome data are computed using reported test statistics or estimates of correlations. However, adjustments could not be made to standard errors to account for within-subject designs as suitable information about withinperson correlations was not available in the studies. None of the within-subject studies reported SDs directly, and we were already making strong assumptions to estimate the missing SDs. In order to adjust for the within-subject design, additional unsupported assumptions regarding the correlations would need to have been made.
Final outcome values served as the primary unit of analysis. For studies assessing changes from baseline as a result of an experimental manipulation, we calculated final values based on either reported data or supplementary data obtained by contacting the study authors. In relation to potential unit of analysis issues arising from studies with multiple eligible comparison groups, our plans are provided below in the Data synthesis section.

Dealing with missing data
We sought data that were missing from reports of included studies by contacting the study authors. Where data were missing due to participant dropout, we conducted available-case analyses and recorded any issues related to missing data within the 'Risk of bias' assessment.

Assessment of heterogeneity
We assessed statistical heterogeneity in results by inspecting a graphical display of the estimated treatment effects from included studies along with their 95% CIs, and by formal statistical tests of homogeneity (Chi 2 ) and measures of inconsistency (I 2 ) and heterogeneity (Tau 2 ).

Assessment of reporting biases
We drew funnel plots (plots of effect estimates versus the inverse of their standard errors) to inform assessment of reporting biases. We conducted statistical tests to formally investigate the degree of asymmetry using the method proposed by Egger and colleagues (Egger 1997). Results of statistical tests were interpreted based on visual inspection of the funnel plots. Asymmetry of the funnel plot may indicate publication bias or other biases related to sample size, though it may also represent a true relationship between trial size and effect size.

Data synthesis
We described and summarised the findings of included studies to address the objectives of the review. We provided a narrative synthesis describing the interventions, participants, study characteristics, and effects of eligible interventions upon prespecified outcomes (see Criteria for considering studies for this review). Our statistical analysis of the results of included studies used a series of random-effects and fixed-effect models to estimate summary effect sizes as SMDs with 95% CIs in terms of each specified outcome. Our planned statistical analysis comprised the following stages: • Stage 1: conduct separate meta-analyses for each product type (food, alcohol, and tobacco) and, within each product type, conduct separate meta-analyses for (i) availability interventions and (ii) proximity interventions.
Then for each meta-analysis: • Stage 2: conduct a meta-regression analysis with study characteristics (including summary risk of bias) as covariates; • Stage 3: conduct a meta-regression analysis with intervention characteristics as covariates; • Stage 4: conduct a meta-regression analysis with participant characteristics as covariates.
Study-level effect sizes calculated based on outcome data from independent within-study comparisons were directly incorporated into Stage 1 meta-analyses. For studies that included three or more eligible comparison groups (e.g. a study of a proximity intervention placing a food product either 1 m, 2 m, or 3 m from participants), we treated each eligible within-study comparison as providing independent outcome data, but adjusted those data to account for the dependency between multiple comparisons as described in the following paragraph. We planned to analyse data from multi-arm studies based on incremental comparisons only. We followed this for availability interventions, whilst for the analysis of proximity interventions, we decided to consider the shortest distance as a comparator against which all other intervention arms would be compared (e.g. 1 m versus 2 m, 1 m versus 3 m, but not 2 m versus 3 m), to allow meta-regression analyses to investigate the impact of increasing differences in proximity and because the nearest point to the participant is the logical comparator in any comparison given the mechanisms posited to underlie the intervention. For studies contributing multiple pairwise comparisons to a metaanalysis, provided the sample size was large enough, each pairwise comparison was included separately. We adjusted the study weights to account approximately for the statistical dependencies between comparisons by dividing the sample size of the common intervention group as evenly as possible between the comparisons. If the sample size for the common intervention group was 1 for any comparison after dividing the common intervention group, we combined intervention groups to give a single pairwise comparison. If there was an even number of groups, we divided the groups in half based on the level (i.e. low or high) of the intervention type (i.e. proximity and availability). If the number of groups was odd, the group left over as the 'middle' level was incorporated into the higher-level group. We did not undertake multivariate analysis to deal with studies with multiple treatment arms as had been proposed as a possibility in the protocol, since the studies with multiple treatment arms had different numbers of arms that were not directly comparable across studies. As a post hoc sensitivity analysis, we repeated meta-analyses but instead entered a single effect estimate for each multi-arm study, obtained using the mean SMD and the mean variance across the multiple comparisons from that study (a conservative approach that will underestimate precision). We planned to exclude a covariate from Stages 2, 3, or 4 of a metaregression analysis if useable data were available from fewer than 10 eligible studies incorporated into the corresponding Stage 1 metaanalysis and/or covariate values did not enable sufficient discrimination between studies (e.g. if covariates are identical, with all included studies using a between-participants design and randomis-ing individual participants). Within each stage of a meta-regression analysis, we proposed to test each covariate separately to identify those variables statistically associated with each outcome. Finally, we planned to estimate and present a meta-regression model that incorporated the set of covariates that best explained statistical heterogeneity observed in the corresponding Stage 1 metaanalysis. We planned to use the following procedure to select and incorporate covariates into this multivariable model: 1. rank those covariates identified as potentially important predictors of the outcome in Stages 2, 3, or 4 in order of the corresponding adjusted R 2 values; 2. starting with the top-ranked covariate, use a stepwise procedure to add each consecutively ranked covariate into the multivariable meta-regression model; and 3. retain a covariate in the multivariable model only if it increases the adjusted R 2 for the multivariable and no collinearity or multicollinearity with other retained covariates is detected. In practice, we conducted meta-regression only on the consumption outcome for proximity interventions, as there were insufficient data (fewer than 10 comparisons) for all other interventions/ outcomes. Furthermore, we conducted only univariate meta-regression analyses. Multivariate analyses were not possible due to a lack of data and given that there were not variables identified that modified the intervention effect within each stage of the analysis. Additional details and results of the meta-regression analyses are reported in the Effects of interventions section. Statistical analyses were conducted in R (version 3.4.2) and metafor (version 2.0-0) (Viechtbauer 2010).

Treatment of multicomponent studies
For included studies using factorial designs to investigate the effects of multiple experimental manipulations, we combined outcome data across groups to capture the main effect attributable to each 'availability' or 'proximity' comparison. For studies of interventions with concurrent components that were unrelated to but intrinsically confounded with the manipulations of interest (namely product availability or proximity), we treated the presence of concurrent components as a study characteristic, indicating the presence or absence of one or more additional intervention components. An example of such confounded concurrent components would be when a product is made less available but also has warning labels added to its packaging (relative to that product being more available and having no additional warning labels). Our primary analyses excluded comparisons where confounded concurrent intervention components were present. We subsequently conducted sensitivity analyses whereby these comparisons were reinstated, in order to assess their impact on the results.

Certainty of evidence
We used the GRADE framework to rate the certainty of each body of evidence incorporated into meta-analyses for (1) selection (with or without purchasing) and (2) consumption outcomes, to indicate the confidence that can be placed in summary estimates of effect (Guyatt 2011; Schünemann 2011). This is an assessment of the likelihood that the true effect will not be substantially different from what the research found. Within the GRADE approach, the certainty of a body of evidence for intervention effects is assessed based on the design of the underlying studies -with RCTs initially considered high certainty -and on a number of factors that can decrease or increase certainty. GRADE criteria for downgrading certainty of evidence encompass study limitations, inconsistency, imprecision, indirectness, publication bias, and other considerations (Balshem 2011). If such a criterion is identified, it is classified either as serious (leading to downgrading by one level) or very serious (downgrading by two levels). The four possible certainty ratings that can be applied range from high certainty (meaning that current evidence provides a very good indication of the likely effect, and the likelihood that the actual effect will be substantially different is low) through to moderate certainty (current evidence provides a good indication of the likely effect, and the likelihood that the actual effect of the treatment will not be substantially different is moderate); low certainty (current evidence provides some indication of the likely effect, but the likelihood that the actual effect will be substantially different is high); and very low certainty (current evidence does not provide a reliable indication of the likely effect, and the likelihood that the actual effect will be substantially different is very high). Two review authors independently undertook duplicate assessment of GRADE, with any disagreements resolved by discussion or by consulting a third review author if necessary to reach consensus.

'Summary of findings' tables
We developed 'Summary of findings' tables using GRADEpro GDT (GRADEpro GDT 2015). These tables comprise summaries of the estimated intervention effect and the number of participants and studies for each primary outcome, and include justifications underpinning GRADE assessments. We planned to present separate summary effect sizes and certainty of evidence ratings for food, alcohol, and tobacco products, and for availability and proximity interventions within each of these product types, but in practice no eligible alcohol or tobacco studies were identified.
Results of random-effects meta-analyses are presented as SMDs with 95% CIs. To facilitate interpretation of these estimated effect sizes, we re-expressed them employing selected familiar metrics of selection or consumption using observational data from a population-representative sample (see Effects of interventions for details) (Hollands 2015; Schünemann 2011).

Sensitivity analysis
In addition to the aforementioned treatment of studies featuring confounded additional intervention components, we also conducted sensitivity analyses to explore the impact of any outcome data that were imputed due to missing data.

Results of the search
The flow of studies through the systematic review process is shown in Figure 2. Electronic database searches were initially run between 1 and 4 March 2016. These retrieved a total of 233,996 study records, including duplicates. Twenty-four additional records in the review had been previously identified from other sources, functioning as a reference set, resulting in a total of 234,020 records. Following removal of duplicates (76,899 records), 157,121 titleabstract records were processed in accordance with the semi-automated screening workflow described in Appendix 2. As a result of this process, 27,116 title and abstract records were screened, of which 121 articles were subject to full-text screening. The electronic database searches were updated between 23 and 27 July 2018. For these updated searches, following removal of 7202 duplicate records, 37,864 title-abstract records were processed in accordance with the semi-automated workflow. This resulted in 2962 title-abstract records being screened, with a further nine articles subject to full-text screening. , respectively, the number of high-fat and high-calorie options available in vending machines (with corresponding increases in low-fat and low-calorie options). One study decreased the number of higher-calorie (relative to lower-calorie) beverages on display within supermarket checkout refrigerators (Foster 2014). The remaining study decreased the proportion of less-healthy (i.e. higher-energy) cooked meal, snack, cold drink, and sandwich options, with a corresponding increase in healthier (i.e. lower energy) options (Pechey 2019). Two availability studies were confounded to some degree with other concurrent interventions within the same physical environment (Fiske 2004; Foster 2014), the former also manipulating the addition of labels, and the latter additionally manipulating the visibility of products (but not meeting our criteria for a proximity intervention). It should be noted that, in order to ensure consistency in treatment and interpretation of effects, the comparisons within our analysis were always coded as reducing the availability of products, irrespective of whether the intervention was conceptualised by the authors as concerning increasing or decreasing availability. Most studies (4/ 6) manipulated snack foods or drinks ( . All of these studies manipulated snack foods or drinks intended for immediate consumption. In these studies, the comparisons concerned relatively small distances, with the greatest distance products were placed at ranging from 0.7 m, Hunter 2018 (S1); Hunter 2018 (S2); Hunter 2019, to 12.2 m, Engell 1996 (S1). Four further studies manipulated the order of products encountered along buffet or lunch lines to increase the distance of the product upon entering that line (Cohen 2015; Greene 2017; Kongsbak 2016; Wansink 2013a), all of which manipulated components of breakfast or lunch meals. Three proximity studies were confounded to some degree with other concurrent interventions within the same physical environment (Cohen 2015; Greene 2017; Kongsbak 2016). Cohen 2015 additionally manipulated placing fruit in attractive containers and other fruit options next to the cash registers, as well as prominently displaying signage promoting fruits and vegetables. Greene 2017 made various changes including to the way in which fruits were presented and labelled. Kongsbak 2016 also manipulated whether salad components were mixed together or placed separately. Similar to our availability analysis, comparisons were always coded as reducing the proximity of prod-ucts, irrespective of whether the intervention was conceptualised by the authors as concerning increasing or decreasing proximity. The included studies of proximity focused on a range of products that can be characterised as healthier in six studies (fruit, vegetables, water) (Cohen 2015; Engell 1996 (S1); Engell 1996 (S2); Greene 2017; Privitera 2012 (S1); Privitera 2012 (S2) . We excluded Wansink 2013a from the analysis due to reporting data that were modelled, with the raw data based on observations unobtainable.

Excluded studies
We excluded 113 studies at the full-text screening stage. Of these, we excluded 76 studies for not featuring an eligible intervention; 27 for not using an eligible study design; nine for not assessing selection or consumption as defined; and one study for not being a report of an empirical study. Excluded studies are listed in the

Risk of bias in included studies
We used the RoB 2.0 tool to assess risk of bias for each of the included studies. A summary of these assessments is provided in Table 1. In terms of overall risk of bias, there were concerns about risk of bias for the majority of studies (20/24), with two of these assessed as at high risk of bias (Musher-Eizenman 2010; Wansink 2013a). A text summary is provided below for each of the six individual components of the 'Risk of bias' assessment. Bias arising from the randomisation process. This was the most common criterion for which risk of bias was apparent, with signifi- We considered one study as at high risk of bias because it could not be ruled out based on the description that participants were allocated to intervention in an alternating sequence rather than as a result of randomisation (Wansink 2013a). Bias arising from the timing of identification and recruitment of individual participants in relation to timing of randomisation. This assessment only applied to cluster-randomised trials (Cohen 2015; Fiske 2004; Foster 2014; Kocken 2012; Langlet 2017), and all five such studies were considered as at low risk of bias for this domain. Bias due to deviations from intended interventions. We judged all studies to be at low risk of bias on this domain, apart from two studies for which significant concerns were identified (Painter 2002; Wansink 2006). These two studies used cross-over designs with short wash-out periods, meaning that it is likely that participants were aware of being exposed to the intervention and the possibility of carry-over effects could not therefore reasonably be dismissed. Bias due to missing outcome data. This was typically judged to be at low risk. There were substantive concerns about risk of bias for one study in which there were substantial missing data (Musher-Eizenman 2010). Additionally, the assignment and effect of missing participants was not detailed. Bias in measurement of the outcome. All of the included studies used objective measures of behaviour, an inclusion criterion for the review. We judged this domain as low risk for all studies. Bias in selection of the reported result. We judged this domain as low risk for all studies. However, it is notable that, to our knowledge, only five of the included studies were preregistered with publicly available study protocols (Cohen 2015; Hunter 2018 (S1); Hunter 2018 (S2); Hunter 2019; Pechey 2019).

Effects of interventions
See: Summary of findings for the main comparison Lower versus higher availability (i.e. fewer versus more options) of food products for changing quantity of food selected or consumed; Summary of findings 2 Lower versus higher proximity (i.e. placed farther away versus placed nearer) of food products for changing quantity of food selected or consumed We have reported results separately for both availability interventions and proximity interventions, for both selection and consumption outcomes. As we identified no study in which alcohol or tobacco products were the target of the intervention, the results of this review relate solely to food. Results of meta-analyses are presented as standardised mean differences (SMDs) with 95% confidence intervals (CIs). Using a similar approach to re-expressing effect sizes in a more familiar metric as we have used previously (Crockett 2018; Hollands 2015), we have also re-expressed SMDs based on estimated average (mean) consumption levels and standard deviations (SDs) among representative samples of the UK population. For this translation, we calculated an estimate of the percentage reduction in energy consumed over a typical snack occasion, given that the included studies typically manipulated snack foods intended for immediate consumption. For selection outcomes, it was assumed that all food that is selected is consumed. We used a mean (SD) of 200 (±63) kilocalories(kcal) as a baseline value, given guidance concerning a 200 kcal threshold for energy consumption from snacks (NHS 2018). These figures were based on daily energy intake from food among UK adults (aged 19 to 64) estimated at 1773 ± 561 kcal by the most recent available years (7-8, i.e. 2014/15 to 2015/16) of the UK National Diet and Nutrition Survey (Public Health England 2018a). However, it is important to note the limitations of such translations (Hollands 2015). Firstly, these re-expressed values relate to UK populations (although readers could translate the results in similar fashion using representative survey data from other countries). Secondly, because such translations necessarily extrapolate beyond the scope of the included studies and data therein, they are intended only to be illustrative for guiding interpretation of the meta-analyses. In this particular case, there is additional extrapolation in assuming that the variance associated with total daily energy intake will be proportionate for lower levels of energy intake.

Effect on selection of lower availability of food products
For our primary analysis, useable outcome data were available for three comparisons involving 154 participants and identified from three food studies that changed either the relative number (proportion) of less-healthy (to healthier) options, or changed the absolute number of different options available (Kocken 2012; Pechey 2019; Roe 2013). Kocken 2012 decreased the number of highcalorie options available in vending machines (with corresponding increases in low-calorie options). Pechey 2019 changed the relative proportion of less-healthy (i.e. higher energy) cooked meal, snack, cold drink, and sandwich options, with a corresponding change in healthier (i.e. lower energy) options. Roe 2013 changed the absolute number of different fruit and vegetable options. Random-effects meta-analysis produced a summary mean effect size (SMD) of −1.13 (95% CI −1.90 to −0.37, P = 0.003), meaning that lower availability of a targeted range or category of food(s) -here being a lower proportion of less-healthy (to healthier) options or a lower absolute number of different options -decreased the amount that was selected, with a large relative effect size ( Figure  3; Summary of findings for the main comparison). Our interpre-tation of the size of this summary effect suggests that if availability was reduced for an assumed average snack occasion of 200 (±63) kcal, adults would select 71 kcal fewer, reducing energy selected by 35.6% (59.9% to 11.7% less). The I 2 statistic (64%) indicates that a substantial amount of the total variance in study-level estimates of this effect was attributable to statistical heterogeneity, which was consistent with differences in the characteristics of the studies within this analysis. When a fixed-effect model was used, the effect was similar: SMD −1.01 (95% CI −1.35 to −0.67, P < 0.001). Assessing evidence of possible publication bias via funnel plots was not appropriate due to the low number of studies. We were unable to conduct meta-regression analysis due to the lack of studies, with fewer than 10 data points for all variables. GRADE assessment indicated that the evidence for this outcome is of low certainty, meaning that current evidence provides some indication of the likely effect, but the likelihood that the actual effect will be substantially different is high. We reached this judgement through consideration of the following criteria. We downgraded the current evidence by one level (i.e. serious limitations) due to study limitations because we judged the study-level estimate of this effect to have significant concerns related to risk of bias. We also downgraded the evidence by one level due to imprecision, be-cause even though the lower CI value indicated a small-moderate effect, the CIs were wide, and the number of participants (sample size) incorporated into this meta-analysis was notably small and did not exceed the optimal information size (i.e. the number of participants generated by a conventional sample size calculation for a single adequately powered trial powered conservatively to detect a small effect size). We did not downgrade the evidence for inconsistency (effect sizes were in a consistent direction with some overlap of CIs, although heterogeneity was considerable), indirectness, or for other considerations including publication bias. No data were imputed for studies included in the primary analysis, therefore the planned sensitivity analysis concerning imputed data was not applicable. We excluded data from two additional studies from the primary analysis for this outcome due to the intervention effect being confounded as part of multicomponent interventions (Fiske 2004; Foster 2014). In a prespecified sensitivity analysis, we reinstated these data, resulting in an analysis of five comparisons, involving 172 participants, identified from five food studies (Fiske 2004; Foster 2014; Kocken 2012; Pechey 2019; Roe 2013). This did not alter the result or interpretation, with point estimates and 95% CIs being similar for both random-effects and fixed-effect models (random-effects SMD: −1.01 (95% CI −1.57 to −0.45, P < 0.001); fixed-effect SMD: −0.97 (95% CI −1.30 to −0.65, P < 0.001)).

Effect on consumption of lower availability of food products
For our primary analysis, useable outcome data were available for three comparisons involving 150 participants in two food studies that changed the absolute number of different options available When a fixed-effect model was used, the mean effect size was larger, with CIs not including zero: −0.84 (95% CI −1.18 to −0.49, P < 0.001). Our interpretation of the size of the summary effect from the random-effects model suggests that if availability was reduced for an assumed average snack occasion of 200 (±63) kcal, adults would consume 35 kcal fewer, reducing energy consumed by 17.3% (40% less to 5.7% more). The I 2 statistic (63%) indicates that a substantial amount of the total variance in study-level estimates of this effect was attributable to statistical heterogeneity, which was consistent with differences in the characteristics of the two studies within this analysis. A sensitivity analysis in which a single average SMD was computed for each multi-arm study produced SMD −0.69 (95% CI −1.63 to 0.24, P = 0.15) in a random-effects analysis based on two results.

Figure 4. Forest plot of the standardised mean difference (SMD) in consumption with higher (intervention 1) versus lower (intervention 2) availability of food products (i.e. more versus fewer options).
Assessing evidence of possible publication bias via funnel plots was not appropriate due to the low number of studies. We did not conduct meta-regression analyses due to the lack of studies, with fewer than 10 data points for all variables. GRADE assessment indicated that the evidence for this outcome is of low certainty, meaning that current evidence provides some indication of the likely effect, but the likelihood that the actual effect will be substantially different is high. We reached this judgement through consideration of the following criteria. We downgraded the current evidence by one level (i.e. serious limitations) due to study limitations, as we judged all study-level estimates of this effect to have significant concerns related to risk of bias. We also downgraded the evidence by one level due to imprecision. Whilst the point estimate indicated a moderate effect on reducing consumption, the CIs were wide and included the possibility of a small effect on increasing consumption. Furthermore, the number of participants (sample size) incorporated into this meta-analysis was notably small and did not exceed the number of participants generated by a conventional sample size calculation for a single adequately powered trial, powered conservatively to detect a small effect size (optimal information size). We did not downgrade the evidence for inconsistency, as whilst statistical heterogeneity was substantial (although not considerable), effect sizes were in a consistent direction, and the meta-analysis result was driven mainly by a single study (Roe 2013). We also did not downgrade the evidence for indirectness, as all included studies assessed participants, interventions, comparators, and outcomes that met the eligibility criteria for this review. We did not specify that any particular characteristics were more informative than others in addressing the objectives of the review, such as those conducted in particular settings, although the included studies for this outcome were from both field, Roe 2013, and laboratory, Stubbs 2001, settings. Finally, we did not downgrade the evidence for other considerations including publication bias because there was no clear evidence of such bias, and we judged that there were no applicable reasons to consider upgrading the certainty of the evidence. Our prespecified sensitivity analyses concerning imputed data meant the removal of data from Stubbs 2001, with only the Roe 2013 data remaining, resulting in an effect size (SMD) of −1.07 (95% CI −1.47 to −0.68). This analysis did not significantly alter interpretation, and represents only a single study, but relative to our primary analysis, the point estimate indicated a larger reduction in consumption, with wide CIs that no longer include the possibility of an increase in consumption. The planned sensitivity analysis concerning additional confounded intervention components was not applicable for this outcome.

Effect on selection of lower proximity (i.e. food products placed farther away)
For our intended primary analysis of selection outcomes for proximity interventions, we identified only one study (Langlet 2017). One comparison (41 participants) found that exposure to food placed farther away resulted in a moderate reduction in its selection: SMD −0.65 (95% CI −1.29 to −0.01, P = 0.045), equivalent to adults selecting 20.5% less energy (40.6% to 0.3% less) (Summary of findings 2). Assessing evidence of possible publication bias via funnel plots was not appropriate due to insufficient studies. Meta-regression analysis could also not be conducted due to insufficient studies, with fewer than 10 data points for all variables. GRADE assessment indicated that the evidence for this outcome is of very low certainty, meaning that the current evidence does not provide a reliable indication of the likely effect, and that the likelihood that the actual effect will be substantially different is very high. We reached this judgement through consideration of the following criteria. We downgraded the current evidence by one level (i.e. serious limitations) due to study limitations because we judged the study-level estimate of the effect to have significant concerns related to risk of bias. We also downgraded the evidence by one level for imprecision because the effect estimate derived from a single small study. We downgraded the evidence a further level for indirectness, because all the data derived from a study conducted in a laboratory setting, meaning that it may be less directly informative to real-world implementation of the intervention. We did not downgraded the evidence for inconsistency or publication bias. The planned sensitivity analysis concerning imputed data was not applicable for this outcome. There were additional useable outcome data from three food studies that were excluded from the primary analysis for this outcome due to the intervention effect being confounded as part of multicomponent interventions (Cohen 2015; Greene 2017; Kongsbak 2016). In a prespecified sensitivity analysis, we reinstated these data, resulting in an analysis of four comparisons (1703 participants). This did not result in an interpretation that differed from the primary analysis. Randomeffects meta-analysis produced a summary mean effect size (SMD) of −0.71 (95% CI −1.08 to −0.33, P < 0.001), meaning that food products placed farther away resulted in a moderate decrease in selection equivalent to 22.4% less energy (34% to 10.4% less) being selected by adults on each 200 kcal snack occasion. This result was identical when a fixed-effect model was used. The I 2 statistic (0%) indicates that none of the total variance in studylevel estimates of this effect was attributable to statistical heterogeneity.

Effect on consumption of lower proximity (i.e. food products placed farther away)
For our planned primary analysis, outcome data were available for . All of these studies increased the distance at which the product was placed from a set point, in all cases being the distance between a chair, table, or desk and where a participant was positioned. Random-effects meta-analysis produced a summary mean effect size (SMD) of −1.30 (95% CI −2.13 to −0.46, P = 0.002), meaning that placing food products farther away decreased the amount that was consumed, with a large relative effect size. This result differed in magnitude when a fixed-effect model was used, showing a reduced summary mean effect size (SMD) of −0.55, with narrower CIs (95% CI −0.68 to −0.42, P < 0.001). However, the I 2 statistic (97%) indicates that most of the total variance in study-level estimates of this effect was attributable to statistical heterogeneity, suggesting that the source of this heterogeneity should be identified. Two studies were responsible for a significant proportion of the observed heterogeneity as a result of their outlying respective summary effect sizes of (SMD) −5.34 and −6.96 (Privitera 2012 (S1); Privitera 2012 (S2)). We have found no clear explanation for why these studies would have generated such extreme, heterogeneous estimates: study, intervention, and participant characteristics did not differ notably from other studies included in the analysis. The estimated effect sizes are larger than we consider to be plausible, therefore these data were removed from the main analysis. Removing these two studies meant that this Our interpretation of the size of this summary effect suggests that that if proximity was reduced for an assumed average snack occasion of 200 (±63) kcal, adults would select 38 kcal less, reducing energy consumed by 18.9% less energy (26.5% to 11.3% less). We consider this revised analysis of 15 comparisons with outlier values excluded to be the primary analysis for this outcome, and is the result reported in the corresponding Summary of findings 2 and used as the basis for subsequent meta-regression analyses and sensitivity analyses described below. A similar effect was estimated when a fixed-effect model was used: SMD −0.45 (95% CI −0.58 to −0.32, P < 0.001). A sensitivity analysis in which a single average SMD was computed for each multi-arm study produced SMD −0.59 (95% CI −0.85 to −0.33, P < 0.001) in a random-effects analysis based on 12 results.
An asymmetrical funnel plot was observed for this analysis ( Figure  6), with Egger's test giving a P < 0.001 (Z = −4.0853), suggesting the possible presence of publication bias (since the larger studies have SMD estimates nearer 0). The determination of possible publication bias informed the GRADE assessment for this outcome.

Potential modifiers of the effect on consumption (metaregression analyses)
For the effect of proximity on consumption, there were sufficient data as per our criteria (i.e. data points from at least 10 studies for at least some extracted variables) to conduct meta-regression analyses to investigate potential effect modifiers. Whilst the majority of candidate variables were excluded due to either insufficient data or the absence of variability in data values between studies, univariable meta-regression analysis was possible for 10 extracted variables, with numerical results presented in full in Appendix 3.
We observed that four of these covariates were associated with the effect of proximity on consumption. We have outlined the stages of the meta-regression analyses below (as described in Data synthesis), and for each stage, have highlighted any variables observed to be associated with the intervention effect. At Stage 1, we conducted the meta-analysis described above, followed at each subsequent stage with a meta-regression analysis. At Stage 2, where we examined study characteristics as covariates, the following three variables were significantly associated with the intervention effect.
• Product-outcome relationship. Effect sizes for lower (versus higher) proximity were larger when the specific product(s) that was manipulated was the only product available to participants, as opposed to there being other unmanipulated products available. It is plausible that the absence of any other products would increase the effect of the intervention, given less potential for its effect to be diluted.
• Summary risk of bias. Effect sizes for lower (versus higher) proximity were larger for studies at high risk of bias, versus both low risk of bias and those where there were some concerns.
• Socioeconomic context. Effect sizes for lower (versus higher) proximity were larger when deprivation status was low, than among studies with samples that were both high and low in deprivation.
At Stage 3, we examined intervention characteristics as covariates, and the following single variable was significantly associated with the intervention effect.
• Absolute difference in proximity. Effect sizes for lower (versus higher) proximity were larger the farther away the product was placed relative to a comparator. Increasing distance resulting in an increased intervention effect is consistent with the theory underlying why the intervention might work.
At Stage 4, we examined participant characteristics as covariates, and found no variables to be associated with the intervention effect. In summary, meta-regression analyses indicated that the intervention effect was greater under four conditions: the farther away the product was placed relative to a comparator; when only the targeted product(s) (as opposed to a wider range) was available; when participants were of low (versus both high and low) deprivation status; and when the study was at high risk of bias. The results of this analysis should be interpreted with caution because the numbers of data points available for each included explanatory variable only barely exceeded the prespecified minimum level for inclusion (i.e. available data from a minimum of 10 studies). Furthermore, the associations cannot be interpreted as causal, and some of the study characteristics were correlated with each other. For example, all of the studies assessed as at high risk/some concerns of bias were in low deprivation contexts (whilst all studies with samples that were both high and low in deprivation were at low risk of bias); and studies where there were other unmanipulated products available tended to be those in which the absolute difference in proximity was greater. GRADE assessment applied to the analysis that excluded outliers indicated that the evidence for this outcome is of low certainty, meaning that current evidence provides some indication of the likely effect, but the likelihood that the actual effect will be substantially different is high. We reached this judgement through consideration of the following criteria. We downgraded the current evidence by one level (i.e. serious limitations) due to study limitations, as we judged the majority of study-level estimates of this effect to have significant concerns related to risk of bias. We did not downgrade the evidence for imprecision because even the lower CI value indicated a small-to-moderate intervention effect, and the number of participants (sample size) incorporated into this meta-analysis was substantial and exceeded the optimal information size. We did not downgrade the evidence for inconsistency (as although heterogeneity was substantial, effect sizes were in a consistent direction with reasonable overlap of CIs) or indirectness. We downgraded the evidence by one level for publication bias because formal assessment of the degree of asymmetry present in a funnel plot suggested its presence.
Our prespecified sensitivity analyses concerning imputed data meant the removal of data from Painter 2002 and Wansink 2006 from the primary analysis. This did not alter the results or interpretation, with point estimates and 95% CIs being similar to our primary meta-analysis (random-effects SMD −0.66 (95% CI −0.94 to −0.37, P < 0.001); fixed-effect SMD −0.46 (95% CI −0.60 to −0.32, P < 0.001)). We excluded data from two studies from the primary analysis for this outcome due to the intervention effect being confounded as part of multicomponent interventions (Cohen 2015; Greene 2017). In a prespecified sensitivity analysis, we reinstated these data, resulting in an analysis of 17 comparisons

Secondary outcomes
Secondary outcomes, specified as selection and consumption outcomes relating to products not manipulated by the intervention, were rarely reported. This was principally because interventions manipulated all the available products, or because outcomes relating to non-manipulated products were not assessed. One availability study included secondary outcomes that met our criteria: Pechey 2019 reported that the intervention resulted in significantly less total energy (−7.2%) being purchased, that is energy from all food categories, whether targeted by the intervention or not. Two proximity studies included pertinent secondary outcomes. Cohen 2015 reported no effect of the intervention on selection and consumption of non-manipulated main meals, and Kongsbak 2016 reported that the intervention resulted in less total energy being selected. Such limited reporting of these outcomes may be expected in laboratory studies featuring single or small numbers of products, but in this body of studies it was also rarely reported in field settings, which may also partly reflect the complexity of capturing and interpreting such data in complex real-world food environments. In sum, data on secondary outcomes were sparse and difficult to compare across studies due to differing study characteristics. There was, however, a small amount of evidence suggesting that compensatory behaviour -for example increased selection or consumption of non-manipulated products -did not occur. Furthermore, there was an absence of clear evidence suggesting that such compensatory behaviour did occur.

A D D I T I O N A L S U M M A R Y O F F I N D I N G S [Explanation]
Lower versus higher proximity of food products for changing quantity of food selected or consumed Patient or population: Adults and children Setting: Field and laboratory settings Intervention: Lower proxim ity of f ood products (placed f arther away) Comparison: Higher proxim ity of f ood products (placed nearer)

Certainty of evidence (GRADE)
Assumed risk: higher proximity of food products (placed nearer)

Summary of main results
The evidence in this review suggests that people select less of a targeted range or category of food(s) when fewer options of that food are available. Because the direction of comparisons within the analysis is interchangeable, they likewise select more when more options are available. However, there was greater uncertainty about the effect of such availability interventions on consumption. A separate body of evidence suggests that people consume less food when products are placed farther away (and likewise more when placed nearer), with a less certain effect on selection. Consequently, these interventions have the potential to have beneficial or harmful effects on health, depending on the characteristics of the food(s) that they focus upon. The summary effect sizes derived from meta-analyses were considerable, suggesting potential impacts of between 17% and 36% on energy selected and consumed on an average snack occasion. Although such estimates are necessarily tentative due to limitations of the underlying data and the assumptions inherent to generating and applying them, if sustained effects of such magnitude were realised and extended to foods consumed over each day, reductions in daily energy intake would have the potential to make meaningful contributions to addressing major risk factors for noncommunicable disease. For example, 10-year weight gain between 1999 and 2009 among adults in England (i.e. 9 kg at the 90th percentile) has been estimated to be equivalent to extra energy intake of around 24 kcal per day over the same period (an amount equivalent to approximately 1.4% of average daily energy intake for UK adults) (Department of Health 2011). Any sustained reductions in daily energy intake exceeding this level are therefore likely to be effective in helping to prevent further weight gain in the population. Whilst these illustrations highlight the promise of these interventions, the sustainability of their effects has yet to be established, with the majority of studies in this review featuring short-term exposures to interventions, and because the certainty of the evidence varied and was assessed as low or very low for all outcomes, we can only have limited confidence in the effect estimates. Importantly, the evidence base for this review was limited in quantity, often severely so, and was entirely absent for alcohol and tobacco products. Furthermore, evidence was sparse for secondary outcomes that could indicate the potential for unintended compensatory behaviour, although there was a small amount of evidence suggesting that this did not occur in response to the intervention and an absence of clear evidence suggesting that it did. Due to the lack of data, we were also unable to satisfactorily address the second objective of the review, concerning potential modifiers of the observed intervention effects (see Overall completeness and applicability of evidence).

Overall completeness and applicability of evidence
The completeness and applicability of the evidence was limited as a result of several characteristics of the evidence base. The synthesised evidence was collected from 24 included studies, with only six reporting availability interventions. In only one primary analysis (the effect of proximity on consumption) did the sample size exceed the optimal information size. The sample sizes weaken confidence that these studies enable us to address the first objective of this review. An additional impact of the limited quantity of evidence is that this reduces the representativeness of the evidence base across a myriad of possible study, intervention, and participant contexts. This means that the extent to which the results of the review apply to other contexts is uncertain. For example, the majority of studies were conducted in the USA, with no studies in LMICs, and participants were typically characterised by low social and material deprivation. These factors limit assessment of social differentiation in effects relevant to health equity. For example, while we have no reason to expect that mechanisms by which exposure to these interventions may influence behaviour will differ substantively and systematically between people living in HICs and those living in LMICs, a range of socio-cultural, economic, and contextual differences between these groups could plausibly modify effects. Studies are needed that focus on these contexts. A further limitation regarding completeness concerns the setting of studies. The majority of included studies were conducted in laboratory settings -which even when relatively naturalistic in their design cannot convincingly replicate uncontrolled, real-world settings -although this limitation does apply differentially to availability and proximity interventions. For availability interventions, while there was a very small number of studies, the majority were conducted in field settings (namely schools, a childcare facility, worksite cafeterias, and supermarkets) and intervention exposures were over prolonged time periods. Despite this, there were insufficient data to draw meaningful conclusions specific to any one type of field setting (e.g. schools or supermarkets), given that contextual characteristics and participant behaviours are likely to differ substantially between these settings. Only four proximity studies were conducted in field settings. Laboratory-based studies of proximity interventions, as is typical for such contexts, usually assessed oneoff exposures or repeated exposures over relatively short time periods, with correspondingly short-term outcomes. They also usually exposed participants to a single, or small range of, snack food intended for immediate consumption, limiting the degree to which such effects can be generalised to complex real-world food environments.
The most notable gap in this evidence base, however, was the absence of any eligible studies investigating effects of these interventions on selection or consumption of either alcohol or tobacco products. This finding is consistent with the small proportion of studies on alcohol and tobacco compared with food products, which we found in a large scoping review of interventions within physical micro-environments (Hollands 2013a; Hollands 2013b). This may be attributable to both a greater interest in, and more opportunities for, intervening on food products due to the broad range that are available, their ubiquity in multiple environments, and the necessity of their consumption. It may also reflect the proportion of research focused on reducing consumption of tobacco and alcohol, compared with food. Research on tobacco and alcohol has tended to consider treatments for the subgroup of the population addicted to those products, whereas studies in relation to food are more likely to take a whole-population approach. Furthermore, tobacco and alcohol are more highly regulated products in terms of where and how they can be sold, which may limit opportunities for research relative to food products. Finally, due to the relatively small amount of available data, it was typically not possible to assess the impact of variations in characteristics between included studies on intervention effects. This meant that it was not possible to satisfactorily address the second objective of this review, namely to assess potential effect modifiers. It was only the effect of proximity on consumption that allowed meta-regression analyses -including only a small number of modifying variables -to be conducted. These analyses indicated that the intervention effect was greater: the farther away the product was placed relative to a comparator; when only the targeted product(s) (as opposed to a wider range) was available; when participants were of low (versus both high and low) deprivation status; and when the study was at high risk of bias. However, because the amount of data available only barely exceeded that which we set as the absolute minimum necessary, and due to their essentially observational nature, these findings should be given considerable caution. Before they can be meaningfully interpreted, they will require confirmation and replication in further research involving larger datasets, but ultimately may prove useful in evaluating, developing, and targeting interventions. Similarly, we were typically unable to examine whether potentially important associations were absent, in other words whether intervention effects were robust to variations in key intervention and participant characteristics. For example, while meta-regression analyses did not find that the proportion of female participants modified the intervention effect, which could add credence to the idea that altering environmental cues has the potential to impact behaviour across populations, we were unable to examine other key characteristics such as age or BMI.

Quality of the evidence
At the level of individual studies, the large majority of studies were subject to significant concerns about risk of bias, reflecting serious concerns about study limitations, compounded by unclear and incomplete reporting of study methods. Commonly, this derived from concerns about bias arising from the randomisation process, but we could not identify any obvious reason to prevent the implementation of unbiased procedures for random sequence generation and allocation concealment or reporting thereof. At the level of the evidence available for each outcome, we accounted for the significant concerns about risk of bias by downgrading each of these outcomes by one level within GRADE assessments. When also considering the full set of GRADE criteria for each outcome (detailed in Effects of interventions), we judged the evidence base to be of low certainty for the effect of availability on both selection and consumption (Summary of findings for the main comparison); low certainty for the effect of proximity on consumption; and very low certainty for the effect of proximity on selection (Summary of findings 2). In sum, this confers, at best, limited confidence in our estimated effects and necessitates due caution in their interpretation. It is noted that Brian Wansink is an author on four of the studies in- contributed data to our primary meta-analyses. This researcher has been subject to multiple retractions of his work due to academic misconduct (Munafò 2018). To date, none of the studies included in this review have been retracted, but should this occur, we will withdraw that study's data from updated meta-analyses conducted as part of a future update. Whilst these retractions introduce additional uncertainty regarding the veracity of other, unretracted studies he has authored, we chose not to report analyses that remove data from any studies authored by Wansink. This would assume that Wansink was principally responsible for the data reported in all studies for which he is an author -an unreasonable assumption without specific knowledge, and potentially unfair to co-authors. Relatedly, it could also set an unwelcome precedent for consistently excluding all data linked by co-authorship to an author who has had papers retracted due to academic misconduct. Finally, we note that for 12 of the studies, potential commercial conflicts of interest were unclear, thus preventing us from eliminating the possibility that the review results could be biased in some way by interests of the study authors.

Potential biases in the review process
The potential for review author error and bias was reduced by involving at least two independent review authors in the selection of studies and the data extraction and study assessment processes.
Whilst it remains possible that we failed to identify all relevant research for inclusion in the review, we used an extensive and highly sensitive search strategy involving a comprehensive range of databases and other sources, as well as backwards and forwards citation searches.

Agreements and disagreements with other studies or reviews
and that also include a quantitative synthesis. Bucher 2016 conducted a systematic review with substantial content overlap with the 'proximity studies' within the current review. Although that review did not meta-analyse the identified studies, the conclusions were consistent with those of the current review, namely that manipulating the order of food products or their proximity can influence food choice. A wide range of other reviews include, but are not limited to, one or both of the target interventions within a scope determined by specific settings or product types. For example, Broers 2017 conducted a systematic review of a range of nudging interventions applied to fruit and vegetable choice, concluding that the largest effect was associated with interventions that altered the placement of products. Grech 2015 reviewed evidence for nutrition interventions applied to vending machines, concluding that there was evidence that altering availability was an effective means of improving the nutritional quality of products purchased. Finally, Cameron 2016 reviewed a broad range of evidence for supermarket-based interventions that included those changing product availability and placement, but the nature of the evidence meant that it was not possible to estimate effects of specific intervention strategies.

Implications for practice
Given the complete absence of evidence for alcohol and tobacco products, the key implications of this review for public health policy and practice concern food products. Furthermore, we identified no evidence from low-and middle-income countries (LMICs), meaning that applicability to those contexts remains uncertain. Whilst, in practical terms, these interventions appear no less suitable for use in LMICs, due to, for example, their likely minimal (fixed and variable) costs, there is as yet insufficient evidence to judge their potential effectiveness or the feasibility of their implementation in such contexts.
This review suggests that policies and practices that alter the availability or proximity of food products could contribute to meaningful changes in the quantities of food that people select or consume, and could be used as part of a wider set of strategies to support healthier food consumption. With the exception of directly controlling availability and proximity, however, assessment of the effectiveness of possible intervention strategies that could achieve this was beyond the scope of this review. Furthermore, due to the limited quantity of current evidence and the low to very low certainty of this evidence, implications for practice are correspondingly tentative.
For interventions that alter availability, capitalising on these effects in a public health context could involve decreasing the absolute number of different options of a range or category of less-healthy food, or decreasing the relative number (proportion) of less-healthy (to healthier) food options that are available within an environment. When the public health goal is to increase selection or consumption of healthier food(s), this could involve increasing the absolute number of different options of a range or category of healthier food, or increasing the relative number (proportion) of healthier (to less-healthy) options. In contrast to the proximity interventions, most of the small set of studies of availability were conducted in field settings, namely schools, a childcare facility, worksite cafeterias, and supermarkets, demonstrating that this is a strategy that is directly transferable to practice and can in theory be implemented in real-world settings. It therefore seems feasible that actions could be taken at a local level -by those who have direct responsibility for the characteristics of environments -whilst broader policy actions in at least some settings could ensure changes to availability. This could include mandating that the nutritional composition of certain ranges or categories of foods available within public-sector establishments like schools or hospitals meet specific nutritional criteria. For example, the Scottish Government and NHS Scotland have introduced the Healthcare Retail Standard (HRS) as a set of mandatory criteria for all retail outlets in all healthcare settings in Scotland, which include requiring at least 50% of products to be from a healthier range (Scottish Government 2015). In another example, as a result of pilot work, the availability of healthier options has been increased in vending machines in 105 National Health Service sites (Public Health England 2018b) For interventions that alter proximity, capitalising on the observed effects could involve placing less-healthy food options in less immediately accessible positions relative to key environmental features (such as farther from entrances, checkouts, or walking or queueing routes), or placing healthier food options in more immediately accessible positions. In contrast to availability interventions, however, the evidence in this review derives principally from studies conducted in artificial laboratory settings. As such, while in principle such interventions would appear directly transferable to practice, their operationalisation and likely impact in real-world environments is less clear. Whilst it is challenging to identify practicable possibilities for intervention and to gauge the potential for higher-level policy actions that could impose subtle or contextspecific changes to layouts of environments (such as changing the order of food presentation in cafeterias), actions could be initiated at the local level by those who have control of those environments. In addition, more comprehensive policy actions could encourage or mandate generalisable changes to environments, at least in certain contexts. For example, while checkout food policies in the UK are currently voluntary (Ejlerskov 2018a), the UK Government intends to consult on plans to ban through legislation the sale of unhealthy confectionery and snack foods at shop checkouts, end of aisles, and store entrances across the retail and out-of-home sectors. Such actions would result in these products being positioned in less accessible positions in shops (Department of Health and Social Care 2018). While they are as yet not directly informed by true experimental evidence, observational data from natural experiments suggest that supermarket polices to reduce less-healthy food at checkouts impact upon purchasing of those foods, namely small packages of confectionery and potato crisps (Ejlerskov 2018b).
There remains considerable uncertainty about the effects of these interventions when implemented under free-living conditions, and their longer-term sustainability. Their effectiveness will be subject to all the challenges and complexities of achieving effective implementation at scale and sustained over time. One such complexity is that scaling up interventions of this kind, increasing their geographic coverage and scope, would involve introducing them into a complex food environment, populated by a multitude of available food and drink products other than those that are being manipulated. This would raise the potential for compensatory consumption or substitution effects (see Implications for research), which the evidence assembled in this review does not sufficiently elucidate.

Implications for research
The key research implication of this review is that more high-quality studies of both availability and proximity interventions in field settings are needed. Studies of these kinds of environmental interventions are viable in real-world settings, as evidenced by existing examples, although feasibility studies attest to the fact that they are highly challenging to implement and conduct (Hollands 2018; Pechey 2019; Vermeer 2009). Future studies should demonstrate improved rigour in conduct and reporting including pre-registration of study protocols that are publicly available, and with fundamental concerns about risk of bias addressed where possible in line with common standards. Furthermore, in order to systematically develop an understanding of the effect of manipulating environmental cues, studies should, where possible, manipulate environmental cues in isolation in interventions that are designed to be unconfounded in terms of their potentially active components (Allan 2017). These new studies should include those focusing on alcohol and tobacco products, for which there was a complete absence that met the inclusion criteria for this review (see Overall completeness and applicability of evidence). These interventions are in principle transferable to these products given the range of both different alcohol and tobacco (and recognised alternative) products and of environments in which these are selected and consumed.
A further key implication of this review is that future studies should be designed to better assess and report the potential impact of these interventions on selection and consumption both over time -with extended durations of intervention exposure and outcome measurement -and for other products available within a given environment but not targeted by a given intervention. This would increase our understanding of potential compensatory or substitution be-haviour, which could concern shifts in selection or consumption to other untargeted food products or categories. For example, a measured reduction in chocolate consumption, in response to an intervention targeting chocolate, could be accompanied by an unmeasured and undesirable equivalent increase in sugary drink consumption. Additionally, an intervention could alter the temporal patterning of behaviour as a result of compensation. For example, a measured reduction in chocolate consumption at midday could be accompanied by an unmeasured equivalent or greater increase in chocolate consumption later in the day. More detailed examination is therefore necessary to enable better estimation of an intervention's overall impact on energy consumption and related outcomes. Given that the current evidence base predominantly comprises laboratory studies that are limited to manipulating and assessing behaviour in relation to single or very limited ranges of snack foods intended for immediate consumption, it is unable to adequately address this issue. Relevant evidence from field studies remains sparse.
When implemented in real-world settings, these interventions are likely to be applied to highly complex ranges of manipulated and non-manipulated products. Although in this review we did break down the availability and proximity interventions into more granular subtypes, these categorisations remain relatively nebulous and may not be satisfactorily descriptive. It will also therefore be important for the research community to develop a more detailed conceptual understanding, and related means of characterisation and reporting of these interventions. Building on work delineating broad types of interventions in physical micro-environments using the TIPPME typology (Hollands 2017a), developments in this area attempt to map the complex parameters of these interventions and provide a conceptual framework for better characterising them (Pechey under review). In future, such developments may enable a more nuanced analysis and understanding of the intervention characteristics that principally determine effectiveness.
These implications for research are derived from reviewing the current evidence base, which derives exclusively from studies conducted in high-income countries (HICs). It is feasible that they may apply similarly to research in LMICs as for HICs, in that, for example, there is no inherent reason why the nature of interventions and study designs need differ when testing these interventions within LMICs. However, the lack of experience in conducting studies of this kind in LMICs allows for the possibility that research issues specific to such settings may emerge as the evidence accumulates.

Cohen 2015
Methods Study design: Between-participants cluster-randomised controlled trial   Eligible supermarkets had to be located in a low-to-moderate income census tract, located in an area of below-average supermarket density, or located in an area having a supermarket customer base with > 50% living in a low-income census tract Exclusion criteria: None reported

Interventions
Intervention type: Availability Type of availability intervention: Relative number (proportion) of less-healthy (to healthier) options: higher and lower availability (in checkout refrigerators) of full-calorie beverages (vs reduced-calories beverages) Manipulated product type: Food Characteristics of manipulated products: Full-calorie beverages in checkout refrigerators. In context of wide range of other products in shops (including other manipulated categories such as milk and frozen meals) Duration of exposure to intervention: > 1 day Study arms: Targeted products were 1) milk, 2) ready-to-eat cereal, 3) beverages (split into in-aisle beverages and checkout cooler beverages for the intervention), and 4) single-serving frozen meals. The intervention consisted of 4 major marketing strategies used across all categories, with placement as the dominant strategy and promotion as the secondary strategy. Strategies included 1) multiple facings: increased the number of facings of the recommended products; 2) prime placement: placed recommended products at eye/arm level and in the middle of the category aisle and reordered types of milk so that 2% milk was located on the left-hand side of the dairy case followed by 1%, skim, and then whole milk; 3) signage: placed call-out signs with the recommended product's name and price, and shelf runners below recommended products; and 4) secondary placement: mimicked shelf strategies (1 and 2) in all secondary placements (end caps, dead space stacks, etc.). In addition, other strategies were used as appropriate to the category, including 5) cross promotion (cereal and beverages only): displayed recommended products in 2 product categories together, through dead space stacks and end caps (e.g. cereal and bananas, soda and water); and 6) taste-testing (milk only): offered free samples of recommended products to increase shoppers' exposure to healthier options. Control supermarkets received no intervention convenience, visibility, and attractiveness were: at least 2 varieties of fruit were offered; fruit was offered in at least 2 separate locations; cut fruits were displayed in small, attractive cups; whole fruits were displayed in a large, attractive fruit bowl at eye level; fruits were labelled with creative names; creative fruit names were displayed on monthly and daily menus; "fruit factoids" were displayed on dry-erase boards at eye level)

Outcomes
Outcomes reported in study: Fruit, vegetable, and milk selection and consumption based on plate waste data; mean number of items selected and consumed; proportion of lunch trays that contained any type of fruit Notes Although this study also randomised 3 of the 10 schools to a vegetable intervention, outcome data for these 3 schools were not reported in this publication -only fruit intervention results were reported. Publication of the remaining data will be monitored in future updates. Secondary outcomes of vegetable and milk selection and consumption reported in this paper were secondary observations in relation to the intervention focused on promoting fruit. Reports that ensuring availability of at least 2 choices of fruit was already being met in most schools, so while proximity was manipulated, availability was seemingly not altered Hunter 2018 (S1)  be favourable or moderately favourable. As long as the 75% criterion was met, foods were not necessarily replaced by the same type of product. Control schools kept the original products This study was conducted in 3 phases, and only data from Phase I were used in this review (reduced availability of higher-calorie products). In Phase II, labels were introduced, and in Phase III, prices were reduced. Purchase of extra products was selected as outcome measure as these were the least-nutritious categorisation of foods "that deliver only energy and no important vitamins or minerals" and relative importance of reducing consumption of high-energy products versus increasing consumption of low-energy products

Notes
Amount of snacks consumed was the selected outcome of interest because the amount consumed is more relevant to health outcomes than whether any were consumed

Musher-Eizenman 2010
Methods Trial registration record at clinicaltrials.gov/ct2/show/nct03252158. Cluster-randomised trial, but data were aggregate/cluster level. During the intervention period, sites were asked to position replacements in the same location, and with as close as possible to the same number of packs as the removed product, and to restock these as usual. Replacement products were priced at their recommended retail price or using the catering providers' normal pricing guidance. Statistical data necessary to input SMD and 95% CIs were provided by study authors in November 2018 Privitera 2012 (S1)

Outcomes
The main outcome measures were changes in units sold and revenue Notes Identified in updated searches in July 2018. Authors contacted 5th October 2018 for additional information as to eligibility and whether necessary data were collected but no response received

Watanabe 2016
Methods Students were randomly divided into 2 groups for a buffet lunch in 2 separate rooms. In 1 room, 16 kinds of foods were ordered, from vegetable foods to protein foods (vegetable-first group), whilst the dishes were in reverse order in the other room (protein-first group) Participants 61 students Interventions Foods ordered from vegetable foods to protein foods (vegetable-first group) versus dishes in reverse order in other room (protein-first group)

Outcomes
Number of consumed foods was compared between the 2 groups.

Notes
Authors contacted for full study report.

Knowles 2017
Trial name or title Investigating the proximity effect in a competitive food environment  Indexes=SCI-EXPANDED, SSCI, CPCI-S, CPCI-SSH Timespan=All years # 4 TS=(rat or rats or mouse or mice or murine or rodent or rodents or hamster or hamsters or pig or pigs or porcine or rabbit or rabbits or animal or animals or dog or dogs or cat or cats or cow or cows or bovine or sheep or ovine or monkey or monkeys) Indexes=SCI-EXPANDED, SSCI, CPCI-S, CPCI-SSH

Indexes=SCI-EXPANDED, SSCI, CPCI-S, CPCI-SSH Timespan=All years
These exclusions mean that the search is focused on the following: Searching in PUBLIC ENVIRONMENTAL OCCUPATIONAL HEALTH (12,220) MEDICINE RESEARCH EXPERIMENTAL In practice, only univariate meta-regression analyses could be satisfactorily conducted. Multivariate analyses were not possible due to a lack of data and given that there were not variables identified that modified the intervention effect within each stage of the analysis. Results of the univariate meta-regression analyses were as follows, with variables displaying significant associations in bold.