November 2024 update:

See an updated version of this research here.

Abstract

What interventions for reducing consumption of meat and animal products (MAP) have been tested and validated in the scientific literature, and what theories of change drive the most effective interventions? We address these questions with a theoretical review and meta-analysis. We find that appeals to environmental and health concerns most reliably reduce MAP consumption, while appeals to animal welfare, studies administered online, and choice architecture/nudging studies generally do not produce meaningful effects. We then outline eight areas where more research is needed and five promising interventions that have yet to be rigorously tested.

1. Introduction

There are strong personal health, public health, environmental, and animal welfare arguments for reducing consumption of meat and animal products (MAP). However, changing people’s eating behavior is a hard problem. This paper approaches that problem with a theoretical review and meta-analysis. 

A previous review by Mathur et al. (2021 b) called on future MAP research to feature “direct behavioral outcomes” and “long-term follow-up.” Our paper shares those commitments. Therefore, while our review is theoretically comprehensive, our meta-analysis looks exclusively at randomized controlled trials (RCTs), for well-understood reasons, that meet the following quality criteria:

1. Measurements of actual consumption of animal products, rather than (or in addition to) measures of attitudes, behavioral intentions, or hypothetical choices.
2. At least 25 subjects in treatment and control groups or, for cluster-randomized studies, at least 10 clusters in total.
3. At least a single day separating the onset of treatment from outcome measurement. This helps identify effects that endure beyond the length of a single interaction and also helps to mitigate experimenter demand effects.

We also required that the full papers be available on the internet, rather than just a summary or abstract, and written in English. We identified 42 such interventions published in 28 papers or technical reports. 

By our count, there have been 21 narrative reviews, systematic reviews, book chapters, and meta-analyses that either focus or touch on MAP reduction from 2017 onwards (See section 2, table 1 for an overview). However, past reviews are either A) organized around particular theories of change, rather than comprehensive of all literature; B) a few years out of date, which means they miss important recent papers; and/or C) not quantitative. Further, while some previous reviews noted heterogeneity in research quality, none made this a major focus. Our paper therefore fills three gaps. First, it is theoretically comprehensive. Second, it offers quantitative meta-analysis. Third, it focuses on the subset of studies whose designs credibly license causal inference on the key quantity of interest.

The remainder of this article proceeds as follows. Section 2 reviews how we assembled our database of policy-relevant MAP reduction research. Section 3 provides an overview of the findings of the six major strands of this literature. Section 4 describes our analytic methods. Section 5 meta-analyzes the assembled studies. Section 6 discusses what we know works, what we know does not work, areas where more research is needed, and promising theories and strategies that have yet to be rigorously tested. Section 7 concludes with proposed next steps for this paper. 

2. Assembling the database

1. First, Benny knew a lot of relevant research because of his work at Allied Scholars for Animal Protection. We read those studies as well as all relevant studies cited in their bibliographies.
2. We located and read 21 previous systematic reviews, starting with Mathur et al. (2021 b) and Bianchi et al. (2018a, 2018b) and Animal Charity Evaluators’ research reports on dietary changes.
   1. Our search for reviews was assisted greatly by posts by Peter Slattery and Emily Grundy summarizing their 2022 review of reviews.
3. We searched the homepages, google scholar pages, and co-authorship lists of researchers with studies in our database.
4. Occasionally, articles’ published pages suggested further reading that seemed promising.
5. Once we had a pretty good list assembled, we emailed Maya Mathur, Jacob Peacock, Andrew Jalil, Gregg Sparkman, Joshua Tasoff, Lucius Caviola, Jacy Reese Anthis, Emma Garnett, Daniel Rosenfeld and Kristof Dhont to see if we had missed any relevant papers. 

Table 1 provides an overview of 21 previous systematic reviews, narrative reviews, meta-analyses, and book chapters that touch on reducing MAP consumption.

Table 1: Review of previous reviews

3. An overview of MAP reduction literature

Researchers who study MAP consumption do so under many banners, e.g. accelerating the transition to an animal-free food system, vegan economics, the psychology of human and animal intergroup relations, moral circle expansion, and dynamic norms and sustainability. The range of journals is similarly diverse, though Appetite, Nature Food, Journal of Environmental Psychology, Food Quality and Preference, and Food Policy are popular venues. While there is no singular disciplinary home to these efforts, social psychology seems to house the plurality. 

Broadly, the literature we’ve found falls into six conceptual buckets (see section 3.1 for an overview of our search process). The first three are about direct persuasion efforts. These interventions share a presumption that people’s conscious concerns have primacy in their eating choices, and thus appeal to concerns about 1) animal welfare, 2) health, and/or 3) environmental impacts and sustainability. 

The second set of theories are about indirect persuasion efforts. These approaches share a presumption that indirect cues strongly influence our eating behavior, whether by manipulating our physical environment, incentives, or sense of self. The three constituent theories here are:

1. behavioral economics approaches (also called “nudges” or “choice architecture”) that, for example, make meat-free choices more salient or physically accessible, or increase the proportion of vegetarian meals sold in cafeterias;
2. economic interventions which manipulate incentives, for instance by making meat more expensive or meat alternatives less expensive;
3. psychological interventions which typically appeal to (and sometimes manipulate) people’s sense of norms.

Some studies combined multiple theories of change, e.g. presented information about both the health and environmental reasons for eating less meat (Jalil et al. 2023) or an appeal to psychological norms alongside a visual ranking of meal choices by their environmental impacts (Piester et al. 2020).

We now review each strand in turn.

3.1 Appeals to animal welfare

Direct appeals to eat less meat for the sake of animals’ wellbeing inform 13 of 42 interventions in our database. These interventions take many forms. Some studies, often run by animal advocacy organizations such as Faunalytics, The Humane League, and Mercy for Animals, distribute pamphlets or booklets on animal welfare issues. Others have people watch advocacy videos, sometimes in virtual reality, or commercial media that touch on animal welfare issues, such as the movie Babe or the Simpsons episode Lisa the Vegetarian. One paper investigates whether an animal’s perceived cuteness affects people’s willingness to eat it.

These studies share a commitment to the idea that people are motivated by animal welfare concerns, but otherwise draw from different disciplines, theories of change, and information mediums. However, as Mathur et al. (2021 b) note, social desirability bias in this literature is likely “widespread.” The typical study in this literature tries to persuade people that eating meat is morally unacceptable, often by confronting them with upsetting footage from factory farms, and then asks them a few weeks later how much meat they ate in the past week. Experimenter demand effects are likely.

Two studies in this strand meet our inclusion criteria and also measure outcomes unobtrusively. The first is Haile et al. (2021), who distributed pro-vegan pamphlets on a college campus, tracked what students ate at their dining halls and find that “the pamphlet had no statistically significant long-term aggregate effects.” The second is Epperson and Gerster (2021), which shows that a “360° video about the living conditions of pigs in intensive farming via a virtual reality (VR) headset” led to a 6-9% reduction in purchased meals that contained meat in university canteens. 

3.2 Appeals to health

Health concerns motivate 9 of 42 interventions in our database. These studies are often conducted and/or written by medical doctors. For example, Emmons et al. (2005 a) assigned individuals who had received a “diagnosis of adenomatous colorectal polyps” (which are potentially precancerous) to either a usual care condition or a tailored intervention that provided counseling and materials on risk factors for colorectal cancer, “including red meat consumption, fruit and vegetable intake, multivitamin intake, alcohol, smoking, and physical inactivity.” The outcome variable was self-reported servings of red meat per week measured at an 8-month follow-up, which the authors dichotomized into “more than three servings per week of red meat” or not. Overall, there was an 18% reduction in this outcome for the treatment group and a 12% reduction for the usual care condition.

One challenge to integrating these results into our database is that they often focus on red meat and/or processed meat consumption rather than MAP as a whole. There is a risk, therefore, that these interventions might induce substitution towards other animal-based products. Klöckner & Ofstad (2017), for example, recommended that subjects “substitute beef with other meats or fish,” which are arguably worse for animal welfare on a per-ounce-of-meat basis (see Mathur 2022 for further discussion). We did not include this study in our meta-analytic database because we cannot clearly deduce its overall effect on MAP consumption. However, we included all red and/or processed meat consumption studies that did not specifically argue for switching to other MAP products. (See Matt-Navarro and Sparkman (forthcoming) for research targeting fish consumption.)

3.3 Appeals to the environment

These studies focus on the environmental harms of consuming animal products and/or promote plant-based alternatives as a more sustainable option. This framing informs 9 of 42 interventions in our database. Environmental arguments are communicated in a plethora of ways, including leaflets, signs in college cafeterias, op-eds, daily reminder text messages, and in-class lectures.

The landmark study in this branch of the literature is Jalil et al. (2023), who randomly assigned undergraduate classes to hear a “50 min talk about the role of meat consumption in global warming, along with information about the health benefits of reduced meat consumption,” and then measured their subsequent food choices at the college’s dining facilities. Overall, they find that students in the treatment group “reduced their meat consumption by 5.6 percentage points with no signs of reversal over 3 years.” No other study in this literature shows well-identified effects enduring this long.

3.4 Behavioral economics: nudges and choice architecture

Behavioral economics/choice architecture interventions focus on nudging people into unconsciously or semi-consciously choosing meat-free meals. For example, these studies might alter how fruits and vegetables are presented at a buffet; how slaughtered animals are presented on a hypothetical menu; or whether a meat or vegetarian meal is the default at a restaurant (the alternative was presented as “available on request”). This strand comprises five interventions and two studies in our database, both with Emma Garnett as first author. These studies found that doubling the percentage of vegetarian meals available and putting a vegetarian meal closer to the entrance in university cafeterias generally increase sales of vegetarian meals.

This literature features some creative interventions that target realistic theories of change but also some startling design limitations. The most concerning is the use of hypothetical outcomes. For instance, Campbell-Arvai, Arvai, and Kalof (2017) intercepted college students on their way to a dining hall “under the pretence of completing a survey about their food preferences,” then led them “to a small conference room” where they were presented with different configurations of menus whose items were selected from options at the dining hall. Students told researchers which food they preferred and then left to go eat their meal, which the researchers did not track. As the authors themselves put it, this design might “be critiqued for not providing actual food choices and thus lacking any real consequences.” Along the same lines, Bacon and Krpap (2018) asked MTurk participants to “imagine a scenario in which they were catching up with a friend for dinner in a nice restaurant one evening during the week…they were also presented with an image of a cozy table in a restaurant.” The main outcome was probability of selecting a vegetarian option from a hypothetical menu.

Second, some of these studies feature a large number of subjects but assign treatment at the level of a restaurant or dining hall and include too few units for meaningful analysis. McClain et al. 2013 and Reinders et al. 2017, for instance, test plausible theories of change in a college cafeteria and a chain of restaurants, respectively, but had just 2 and 3 units in their respective treatment arms. Both studies did not meet our inclusion criteria but offer plausible theories and promising designs for future replications. Another very nice study (Berke and Larson 2023) randomly assigns folks who are attending an MIT Media lab event, which serves free food, to see either a menu with vegan/vegetarian labels or no labels (all meals were vegetarian or vegan); the authors find that labels significantly decrease the proportion of vegan meals selected. We did not include this study because it lacks delayed outcomes, but we find its underlying theory very plausible. 

See Bianchi (2018 b) for a thorough review of choice architecture interventions.

3.5 Conventional economics: price manipulations

Economic manipulations seek to alter the explicit incentives behind MAP consumption. This is an underdeveloped body of research, informing just 1 of 42 interventions in our database. That study (BIanchi 2022) provides free meat-free substitutes to participants, along with “information leaflets about the health and environmental benefits of eating less meat,” recipes, and success stories from people who reduced their meat consumption. Four weeks after the intervention concluded, treated subjects reported that they ate an average of 38 grams less meat per day than those in the control group (about 11 oz per week).

Two studies in this field presented interesting, plausible theories of change but had design limitations that led us to exclude them from our meta-analysis. First, Vermeer et al. (2010) surveyed people at a fast food restaurant and contrasted two pricing schemes, one where larger sizes were cheaper on a per-ounce basis and one where price-per-ounce was held constant. They found no effect on consumers’ intended portion size purchases, but the real prices were not altered and no real food purchases were measured. As the authors note, “[m]ore research in realistic settings with actual behaviour as outcome measure is required.” Second, Garnett et al. (2021) introduced a small price change at a “college cafeteria in the University of Cambridge (UK), introducing a small change to the price of vegetarian meals (decreased by 20p from £2.05 to £1.85) and meat meals (increased by 20p from £2.52 to £2.72).” The intervention had no main effect on meat sales but increased sales of vegetarian meals by 3.2%. However, treatment and control had just one cluster apiece. This study is an excellent candidate for replication.

3.6 Psychological appeals

MAP reduction studies drawing on social psychological theories comprise 14 of 42 interventions in our database. These studies typically try to normalize vegetarianism and veganism by creating a perception that eating plant-based meals is consistent with social norms. To do this, researchers might put up signs that say things like “More and more [retail store name] customers are choosing our veggie options,” or “The garden fresh veggie burger is a tasty choice!” One study told participants that people who eat meat are more likely to endorse social hierarchy and embrace human dominance over nature, thus making them out to be a counter-normative outgroup.

Other studies conducted drawing on social psychological theories include an app that monitors people’s meat-free pledges on their phones, or a combination of norm-setting and messaging seeking to promote self-efficacy and the perceived feasibility of eating less meat.

A strong study in this category is Sparkman and Walton (2017), who presented people waiting in line at a Stanford cafeteria the opportunity to participate in a 'survey' in exchange for a meal coupon, where the survey presented one of two norms-based messages: a 'static' message about how "30% of Americans make an effort to limit their meat consumption," or a dynamic message emphasizing how behavior is changing over time and that vegetarianism is taking off among participants' peers. The authors find that 17% of participants in the static group ordered a meatless lunch vs. 23% in the control group and 34% in the dynamic norm group.

For an overview of psychological theories of vegetarianism, see Rosenfeld (2018).

4 Meta-analytic methods

For primers on reading and writing meta-analyses, see Frank et al. 2023, chapter 16, or Lakens 2022, chapter 11.

4.1 Coding the database

Condensing an intervention to an estimate of average treatment effect and associated variance sometimes involves judgment calls. Here are the general guidelines we followed:

1. We take the outcome that most clearly maps to changes in actual consumption behavior.
2. We take the latest possible outcome to test for the presence of enduring effects, and our sample sizes are taken from the same measurement wave.
3. For cluster-assigned treatments, our Ns are the number of clusters rather than participants. This includes studies that cluster by day (e.g. everyone who comes to a restaurant on some day gets treated).
4. We convert all effect sizes to estimates of standardized mean differences: Average Treatment Effect (ATE) / standard deviation (SD).
5. When possible, we calculate ATE using difference in differences $\left(\right(T_{T2}-T_{T1})-(C_{T2}-C_{T1}\left)\right)$, which we prefer to difference in means ($T_{T2}-C_{T2}$) because it leads to more precise estimates. When pretest scores aren’t available, we use difference in means.
6. When possible, we standardize by the SD of the control group, a measure called Glass’s Delta (written as ∆). We prefer Glass’s Delta to Cohen’s d, a measure that standardizes by the SD of the entire sample, because we want to to avoid any additional assumptions about equivalence of variance between treatment and control groups. When we don’t have enough information to calculate ∆, we use d.
7. For conversions from statistical tests like t-test or F-test, we use standard equations from Cooper, Hedges and Valentine (2009). The one exception is our difference in proportions estimator, which, to the best of our knowledge, Donald P. Green first proposed for a previous meta-analysis. See our d_calc.R function on GItHub for specifics.
8. When authors tell us that results were “not significant” but don’t specify more precisely, we call the effect type "unspecified null" and record it as ∆ = 0.01.

4.2 Meta-analytic methods

Our meta-analysis employs a random effects model rather than a fixed effects model, for reasons explained here. Our code mainly uses functions from the metafor and tidyverse packages in R as well as some custom wrappers that Seth wrote for previous meta-analyses.

The coefficients we report are: 

• Glass’s Delta (∆), which indicates a meta-analytic estimate: a weighted average of many point estimates, where larger, more precisely estimated studies influence the average proportionally more than smaller ones.
• Beta (β), a regression coefficient. Linear regression tells you E(Y | X), i.e. for some value of X (or many Xs), the expected value of Y. We report this coefficient when we discuss publication bias or the effects associated with covariates.
• SE (standard error) is the standard deviation of the sampling distribution, e.g. ∆ or β. Smaller standard errors mean more precise estimates.
• P-value, a measure of statistical significance. See Lakens (2022), chapter 1 for an overview.

5 Meta-analysis

Section 5.1 provides descriptive statistics about our database. Sections 5.2-5.8 are our pre-registered analyses reported in the order we originally intended. Sections 5.9 and 5.10 are exploratory analyses we came up with after writing our pre-analysis plan.

5.1 Descriptive overview of the database

Our database comprises 28 papers that detail 42 interventions. For interventions with assignment at the level of the individual, the average sample size is 427 participants, and the average cluster-assigned intervention has 64 clusters (the equivalent median numbers are 214 and 54, respectively). 

Twenty-seven interventions take place exclusively in the United States — 20 in person and 7 online with US participants. An additional seven take place in the United Kingdom and three take place in Italy. Australia, Germany, and Canada have one intervention each, while one multisite intervention takes place in the UK, Germany, and, Australia, and one intervention recruits internet participants in the US, UK, Canada, Australia, and “other.”

Twenty-six interventions take place at colleges or universities, while twelve look at adults (18+), and one specifically looks at older adults (40+). One intervention looks at people of all ages (including children), while one looks at women ages 13-25. Sixteen interventions take place on a US college campus.

23 of 42 outcomes are self-reported. These range in granularity from reporting whether subjects had ≤ 3 servings of red meat in a given week (Sorensen et al. 2005) to food questionnaires asking participants to recall everything they recently ate, e.g. in the past 24 hours (Feltz et al. 2022) or the past week (Mathur et al. 2021 a).

The 19 outcomes that are not self-reported are typically recorded at a restaurant or college dining hall. Most are straightforward records of how many meals sold did or did not have meat (Coker et al. 2022, Garnett et al. 2020). By contrast, Piester et al. (2020) affixed menus with “images of zero to five leaves, with more leaves indicating greater sustainability” and then compared the average leaf ratings of meals purchased by the treatment and control groups.

5.2 Overall effect

The overall effect of this literature is small, but statistically significant and precisely estimated: ∆ = 0.131 (SE = 0.03), p < 0.0001. By convention, ∆ = 0.2 is considered to be a “small” effect size, though see Funder and Ozer (2019) for critical discussion.

Another way to consider these results is to take these papers at their word on whether they produced backlash, null, or positive results. Across the 42 interventions reviewed here, 21 report positive, statistically significant results and 16 report null results. However, we don’t observe meaningful backlash effects. Although 5 of 42 interventions report more MAP consumption in the treatment group than in the control, none of these effects were statistically or substantively significant.

Figure 1 presents these results graphically. 

5.3 Tests for publication bias

See here and here for primers on publication bias, also called the file drawer problem, in meta-analyses. 

We find mixed, inconclusive evidence on publication bias. First, as noted before, half of the interventions in our dataset yield null or negative results, which suggests that insignificant and null findings in this literature are able to see the light of day. Second, the relationship between standard error and effect size is small and insignificant: β = -0.0236 (SE = 0.292). (This essentially means that smaller, noisier studies have not been contradicted by larger, better-powered results.)

We do, however, find a moderate though statistically insignificant relationship between a paper’s having a DOI (digital object identifier), which generally means that it has been published in an academic journal, and effect size: β = 0.11382 (SE = 0.07635). In our dataset, the thirty interventions from papers with a DOI have an meta-analytic effect of ∆ = 0.175 (SE = 0.041), p = 0.0002 while the ten studies without a DOI have a meta-analytic effect of ∆ = 0.038 (SE = 0.012), p = 0.009. This might suggest that a study needs to have positive results to be published in a peer-reviewed journal. However, we don’t read too much into this, because many of the studies without DOIs are published by vegan advocacy organizations such as Faunalytics, The Humane League, and Mercy for Animals, which, to their credit, publicize their null results, and sometimes critically re-examine their own findings.

5.4 Differences by assignment, theory and self-report

5.4.1 Cluster-assigned interventions show smaller effects on average

The 14 interventions where treatment is cluster-assigned show much smaller effects on average: ∆ = 0.036 (SE = 0.025), p = 0.181, versus ∆ = 0.57 (SE = 0.037), p = 0.0002 for the 28 interventions where treatment was assigned at the level of the individual.

5.4.2 There are large differences in efficacy between theoretical approaches

Table 2 presents, for each of the six theoretical approaches outlined in section 3, the number of constituent interventions, the average meta-analytic effect, the standard error of that estimate, and stars corresponding to that estimate’s statistical significance. Note that the total N of these categories won’t equal 42, because some interventions combine multiple theoretical approaches.

Table 2: differences in effect size by theoretical approach. ​​* < .05; ** < .01; *** < .001.

Based on these results, it seems that appeals to animal welfare are the least effective category of interventions. Likewise, the aggregated effect of the choice architecture approach is substantively small and not statistically significant. Psychological appeals also do not meet the conventional standard for a ‘small’ effect size in the behavioral sciences. 

The most robust evidence for changing habits comes from appeals to health and the environment. Here, a reasonably sized collection of studies suggests a small but precisely estimated effect on MAP consumption. Last, manipulating economic incentives seems to produce the largest effects, but this is not a robust finding as it is drawn from just one paper.

5.4.3 The effects of self-reported outcomes

In a finding that very much surprised us, self-reported outcomes are systematically smaller than those measured obliquely.

Table 3: differences between self-reported and obliquely reported outcomes. ​​* < .05; ** < .01; *** < .001.

Taking these results at face value, social desirability bias is much less of a concern in this literature than we had believed. This point merits more thinking.

5.5 Do leaflet studies work? 

Four interventions in our dataset test leafleting and find an overall effect of ∆ = 0.038 (SE = 0.011), p = 0.0377. Based on this finding, leafleting is not an effective tactic.

5.6 How do studies administered online compare to in-person studies?

The eight interventions administered online have an average meta-analytic effect of ∆ = 0.048 (SE = 0.013), p = 0.008. By contrast, the 34 interventions conducted in person have an average meta-analytic effect of ∆ = 0.166 (SE = 0.013), p = 0.008. In other words, in-person interventions are about 3.45 times more effective than those administered online; but if an online intervention could reach four people for the price it would take to reach one in person, then online distribution might be more cost-effective. Nevertheless, ∆ = 0.048 is so small that we think this line of work is not fruitful.

5.7 Any relationship between delay and outcome?

Days of delay between treatment and measurement has essentially zero relationship with effect size: β = -0.00002.

5.8 What about publication date? 

Effect sizes seem to be getting smaller every decade. The four interventions published in the first decade of this millennium have an average meta-analytic effect of ∆ = 0.187, compared to ∆ = 0.143 for the 14 studies published in the 2010s and ∆ = 0.123 for the 24 studies published from 2020 onwards. One interpretation for this finding is that contemporary studies tend to be more credibly designed and implemented, and post-credibility revolution studies are more likely to find smaller but more replicable results. 

The analyses we present below were not pre-registered but struck us as interesting questions while working on the analysis.

5.9 Effects on college students vs. adults vs. other populations

Table 4 presents the average meta-analytic effects for college students, adults, and other populations (comprising two interventions, one with women ages 13-25 years and one with people of all ages).

Table 4: Differences in effect size by population. ​​* < .05; ** < .01; *** < .001.

These results suggest that extant interventions produce the largest changes for university students. 

5.10 Effects by region

Table 5 presents the meta-analytic results of studies in the United States, the United Kingdom, Italy, and everywhere else:

Table 5: differences in effect size by location. * < .05; ** < .01; *** < .001.

These results surprised us: we don’t have a clear theory for why studies in Italy showed the largest effects and studies in the US showed comparatively small results. However, we don’t read much into this because of the small Ns for the non-US categories.

6 Discussion

Overall, we’re optimistic about the state of MAP reduction research. 

On the one hand, we need more credible empirical work. With just 28 papers and 42 interventions meeting pretty minimal quality standards, nothing in our analysis should be considered especially well-validated. On the other hand, recent MAP reduction papers tend to bring careful, design-based approaches to the problems of measurement validity, social desirability bias, and verisimilitude. The trend, therefore, is towards increasingly credible work. However, even the best of these studies would benefit from out-of-sample replication to help us understand where and for whom the most promising interventions work. 

6.1 What works to reduce MAP consumption?

In general, appeals to health and the environment appear to reduce MAP consumption, albeit not by very large amounts. Moreover, we have a lot more confidence that these appeals work for college students than for the general population because of the results from Jalil et al. (2023). Still, we can only learn so much from one experiment at one college. We recommend replication and extension.

6.2 What doesn’t work to reduce MAP consumption?

Our review suggests that leafleting studies, studies administered online, appeals to animal welfare, and choice architecture/nudging studies generally do not move the needle on reducing MAP consumption. 

We are disappointed by the lack of efficacy of appeals to animal welfare. We want people to care about animals and their needs for their own sake, not just whether eating them is good or bad for our health and welfare. It seems we have our work cut out for us in making that message persuasive.

We also wish to caveat that many of the most interesting choice architecture interventions did not meet our inclusion criteria, but well-powered, randomly assigned versions of those interventions could be worth pursuing, e.g. Malan et al. (2022), Hansen et al. (2019), Kongsbak et al. (2016), and Gravert and Kurz (2019).

Additionally, we find the lack of backlash effects on MAP consumption encouraging.

6.3 What we still don’t know

It is striking to us that there have been nearly as many papers aggregating and summarizing MAP reduction research — 22 including this one, with two more that we know of on the way — as there have been RCTs meeting minimal quality standards. Here are eight areas we hope to see illuminated by future work. 

1. What interventions work to change behaviors for adults and children?
2. We lack rigorous evaluations of MAP reduction efforts in Latin America, Asia, and Africa.
3. Piester et al. (2020) find that food sustainability labels had a significant impact on women but very little impact on men. Should anti-MAP strategies generally be gender-tailored? (See Veul 2018 for further discussion.)
4. How much is animal welfare advocacy activating disgust avoidance  vs. empathy for animals? e.g. If videos of farmed animal lives show especially squalid or pathogenic living conditions, or if pamphlets about dairy cows  talk about the allowable level of blood and pus in milk products, which theoretical perspective are these interventions embodying, or could empathy and disgust be compared to one another?
5. Theoretically, we’d get equivalent impacts from causing 100 environmentally-conscious people to reduce their MAP consumption by 1% each and causing 1 omnivore to go fully vegan. However, the likely responders might be different populations. How do we tailor our messaging accordingly?
6. Because many of the studies that appeal to environmental and/or health concerns asked about red and/or processed meat consumption, we’re not sure that they reduce consumption of MAP in general. (The exception is Jalil et al. 2023, who measure effects on red meat, poultry, and fish.) What sorts of interventions might we design to improve the welfare of dairy cows, eggs-laying hens, or crustaceans?
7. What is the elasticity of demand for MAP? Our sample, unfortunately, does not allow us to estimate this — we would need many studies of price changes — but if we take the price, taste and convenience theory of change seriously, this is a critical parameter. It seems backwards that there have been many more behavioral economics studies on MAP consumption than well-identified economics studies. (See here and here for observational work on the subject).
   1. A great starting point would be to replicate Garnett et al. (2021), with 1) treatment randomly altered at the level of a week rather than in chunks of 4-5 weeks; 2) for at least ten weeks total; and 3) at multiple sites/cafeterias.
8. Do changes to menus or restaurant layouts have effects on treated consumers a week or two later, rather than just the day of? Most studies with these designs only measure outcomes while treatment is being administered or during the control period, but we also care about lasting changes in habits. 

We also note that while many studies in our dataset partnered with university dining halls, only one (Sparkman et al. 2020) partnered with a grocery/restaurant delivery or meal prep service (which “abruptly closed” in the middle of their experiment). We think this is a promising strategy for deploying large-scale interventions and measuring real-world behavior. Perhaps someone at the economics team at Instacart is interested in pursuing this?

6.4 Next steps for researchers: five promising theories of change that call for rigorous, large-scale testing

1. Intergroup contact. Broockman and Kalla (2016) show that a brief conversation about trans rights, with either a trans or cis canvasser, reduces transphobia for at least 3 months and increases support for a nondiscrimination law. Would a face-to-face conversation about vegan issues, either with a vegan or not, change eating behavior, and/or voting patterns on animal rights bills, e.g. Proposition 12 in California?
2. Extant research evaluating protests has generally measured attitudes toward protests. What about effects on MAP consumption, either for witnesses or participants? Perhaps researchers can identify some mechanism that creates exogenous variation in whether people attend or witness a protest. Alternatively, researchers could randomly assign some on-the-fence participants free transport to a protest, and then send them a coupon to a meal delivery or grocery delivery service a month later and observe whether they select non-meat options.
3. What is the effect of high-intensity vegan meal planning? For instance, researchers could randomly assign 100 people to participate in https://www.swapmeat.co.uk, have them fill out periodic food diaries, and 3/6/9 months after, send them coupons to a grocery delivery service and observe their purchases.
4. Two intriguing papers asks people to imagine contact with a farm animal and then gauge their attitudes and intentions. How about real contact with a farm animal or a visit to a farm sanctuary? For example, researchers could offer a lottery to students at SUNY New Paltz or Vassar for a free tour at Woodstock Farm Sanctuary, then mail them a coupon to a local cafe with vegan options and track their purchases.
5. Blind taste tests, e.g., have 100 people taste either meat or a meat alternative, then send them a coupon for either meat or the alternative and track what they buy.

7. Conclusion: next steps for this paper (and how you can help)

This post is effectively a pre-preprint of the academic article we aim to publish. You can help us with this in a few ways.

1. If you know of any studies we missed, please let us know!
2. If you have further quantitative analyses you’d like to see, we welcome comments on this post. You can also open an issue or PR on the project’s GitHub repo.
3. We have a lot of work ahead of us to get this article properly formatted, submitted to a journal, through peer review, etc.
   1. If you work at a grantmaking institution (or have one to recommend) and are interested in supporting this project, we’d be glad to hear from you.
      1. If you are an academic with an aptitude for getting papers to the finish line, we’d be happy to discuss co-authorship! We have our eyes on Behavioral Public Policy, Psychology of Human-Animal Intergroup Relations, or Psychological Science in the Public Interest.
         1. Likewise, if you are a journal editor and you think your venue would be a good home for this project, please be in touch.

Thanks for reading. Comments and feedback are very welcome!

Statement on additional materials

Our analysis code, data, and pre-analysis plan are available on GitHub, including excluded_studies.csv, which lists the studies we considered but didn’t end up including, as well as a PDF of our appendices. 

Our pre-analysis plan is available on the Open Science Framework. 

Our code and data are also available on Code Ocean, where they can be rerun from scratch in a frozen, code-compatible computational environment.

Acknowledgements

Thanks to Alex Berke, Alix Winter, Anson Berns, Hari Dandapani, Adin Richards, and Matt Lerner for comments on an early draft. Thanks to Maya Mathur, Jacob Peacock, Andrew Jalil, Gregg Sparkman, Joshua Tasoff, Lucius Caviola, and Emma Garnett for helping us assemble the database and providing guidance on their studies.