Beyond all or nothing: The impacts of breastfeeding promotion

Key takeaways

• Breastfeeding promotion programs aim to increase exclusive breastfeeding rates, often through behavioral interventions such as community counseling and education programs. In addition to affecting exclusive breastfeeding rates (generally an outcome of interest in these studies, for which treatment effects are reported), such interventions can affect rates of other breastfeeding intensity levels, including predominant, partial, and non-breastfeeding. Thus, such programs can be understood to affect the distribution of breastfeeding intensities, which we investigate in this report. [more]
• Breastfeeding intensity data are usually collected through maternal self-report, using survey questionnaires. These data are susceptible to significant recall bias and social desirability bias, but it appears infeasible to adjust already-collected data for such bias because social desirability varies significantly across contexts. [more]
• We took a two-pronged approach to analyzing the effects of breastfeeding promotion programs on population distributions of breastfeeding intensity. We both investigated the limited quantitative evidence from the relevant experimental literature and synthesized relevant expert insights from five interviews. [more]
• None of the experts we interviewed were willing to comment directly on distributional shifts in breastfeeding intensity induced by typical breastfeeding promotion programs, and all said that there was very little evidence about this topic. However, they broadly commented on several relevant themes: empirical and data limitations, breastfeeding intensity transitions over time, impact pathways and barriers to breastfeeding, and the disadvantages of breast milk alternatives and complements. [more]
• We identified three relevant breastfeeding promotion randomized controlled trials in low- and middle-income countries that report outcomes on breastfeeding intensity changes as four discrete categories: exclusive, predominant, partial, and none. Using data from these trials, we analyzed changes in these category sizes for treatment and control groups to infer treatment effects on changes in the distribution of intensity, though we acknowledge this approach is imperfect, due to the small number of relevant trials, methodological issues related to self-report and recall, and the insufficient granularity of breastfeeding intensity categories. [more]
• Our rough analysis suggests that promotion programs likely increase breastfeeding intensity among women of all counterfactual intensities of breastfeeding (medium confidence). We think that it may be more likely to cause women of higher counterfactual intensities to go up in intensity category (low confidence), but since the data cannot show within-category effects, that does not necessarily mean a particular group experiences greater actual intensity change due to intervention. We also considered whether baseline intensity might interact with the distributional effect of programs. Our guess is that the baseline intensity of breastfeeding does not have a large effect on how evenly distributed a program’s impact is among individual mothers with different counterfactual intensities (very low confidence). [more]
• From the available data, it was difficult to draw many conclusions about age cohort effects. It seems that increases in breastfeeding intensity persist across the board due to promotion programs even as the infant grows (i.e., across age cohorts; low confidence). However, it appears that at older infant ages (e.g., six months), mothers at counterfactually lower breastfeeding intensities are less likely to respond to intervention by going up in breastfeeding intensity category (very low confidence), and that a greater proportion of mothers who do switch into exclusive breastfeeding do so from the lowest intensities (none, partial), rather than from predominant breastfeeding (very low confidence). [more]
• Given data limitations, we also looked into non-causal evidence of breastfeeding program impacts by age, as well as the evidence of the health effects of various levels of breastfeeding intensity on children at different developmental stages. Breastfeeding promotion programs have varying levels of effectiveness in encouraging early initiation, exclusive breastfeeding, and continued breastfeeding practices across different contexts and age ranges. The health benefits of breastfeeding appear to be strongest in early infancy and gradually decrease over time, with benefits including (but not limited to) immunity, infection prevention, and growth. The evidence becomes less definitive for breastfeeding beyond 12 months. [more]
• While there is limited high-quality evidence directly comparing breastfeeding program impacts across different geographical contexts, observational studies suggest significant variation in program effectiveness based on local conditions, baseline breastfeeding practices, and implementation environments. Global breastfeeding rates show substantial regional disparities, with some areas like sub-Saharan Africa having particularly low baseline rates in certain countries, and notable urban-rural divides in breastfeeding practices. Cultural factors, including traditional practices, religious customs, community norms, maternal education, and workplace conditions, play significant roles in shaping baseline breastfeeding behaviors and potentially influencing program effectiveness across different geographical contexts. [more]
• GiveWell’s current cost-effectiveness analysis already explicitly accounts for multiple pathways to reducing all-cause mortality from breastfeeding promotion. We think the model could potentially benefit from greater age stratification and consideration of improved child growth/reduced stunting. In addition, we identified an inconsistency in GiveWell’s modeling: based on the expert view that a reduction in enteric infection is the main mechanism through which breastfeeding promotion reduces all-cause mortality, GiveWell uses diarrhea morbidity reductions as the primary input to estimate all-cause mortality benefits; however, enteric diseases are not modeled as the top cause. This inconsistency suggests that the model may need to be revised. We outline three possible ways forward: (1) keep the current model and reframe diarrhea morbidity as a general proxy for disease risk; (2) adjust assumptions to weight enteric infections more heavily; or (3) replace diarrhea morbidity with broader morbidity inputs. [more]
• Breastfeeding health outcomes for the infant include lower rates of diarrheal and waterborne illness (and associated mortality), respiratory illness, and non-communicable diseases, as well as improved growth and long-term outcomes. There appears to be a dose-dependent relationship between breastfeeding intensity and health outcomes—with exclusive breastfeeding generally showing better results than partial breastfeeding—and we think there is likely to be a sharper boundary between predominant and exclusive breastfeeding in lower-resource settings that lack reliable access to clean water. However, the exact shape of this relationship and the mechanisms behind it remain unclear due to limited high-quality evidence. [more]

1. What are the effects of breastfeeding programs on population distributions of breastfeeding intensity?

Background on breastfeeding intensity

Several categories of breastfeeding intensity are defined by the World Health Organization (Figure 1). In this report section, we will refer primarily to the following categories, for consistency with outcome reporting in most relevant studies:

• “Exclusive” or “exclusive breastfeeding” (as defined in Figure 1)
• “Predominant” or “predominant breastfeeding” (as defined in Figure 1)
• “Partial” or “partial breastfeeding” (equivalent to “complementary feeding” in Figure 1)

Figure 1: Breastfeeding intensity category definitions

Note. From World Health Organization (2008), p. 4.

Related to the above definitions, we will further refer to “any” (or “any breastfeeding”) and “none” (or “non-breastfeeding”):

• “Any” or “any breastfeeding” (referring to the sum of “exclusive,” “predominant,” and “partial”).
• “None” or “non-breastfeeding” (referring to feeding practices that do not involve any breastfeeding, e.g., exclusive formula/bottle-feeding)

We encountered quantitative definitions of breastfeeding intensity (such as percentage of feedings that are breast milk) in the high-income country (HIC) literature (e.g., Bonuck et al., 2014). However, this appears to be rare in the low- and middle-income country (LMIC) literature, as we did not come across quantitative breastfeeding intensity data in the LMIC studies we reviewed.

Most studies of breastfeeding and breastfeeding promotion focus on exclusive breastfeeding (EBF) as a binary metric. EBF is associated with the most robust health benefits for infants, making it a highly relevant metric for evaluating health outcomes, and causing some to refer to EBF as the “gold standard” (Zhang et al., 2021). Additionally, EBF is a clear metric that is relatively easier to define and measure compared to breastfeeding intensity, which involves multiple overlapping categories and requires more nuanced data collection. Furthermore, many studies, particularly those conducted in low-resource settings, may lack the time, funding, or methodological rigor to gather this level of detail.

We therefore found much less information on breastfeeding intensity than on EBF specifically, and our impression is that many experts are reluctant to speak plainly about the relative importance of various intensities, and about the distributional effects of breastfeeding promotion “up the chain.” We compiled some findings on EBF promotion in Appendix A, but focus on studies comparing breastfeeding intensities for the majority of this report.

Issues with breastfeeding intensity measurement

Breastfeeding intensity data collected in breastfeeding research trials are generally considered poor-quality. Breastfeeding intensity is primarily measured through participant-reported outcomes over potentially long recall periods, and behavioral intervention programs are necessarily non-blinded. As with other forms of self-reported data, most breastfeeding intensity data is susceptible to significant bias, which can be categorized roughly as falling into two categories (partially paraphrased from Stewart et al., 2024):

• Recall bias: Mothers may inaccurately recall the timing of the introduction of complementary liquid and solid foods. Mothers in the treatment group may be primed to think more about their feeding practices and thus recall more accurately than mothers in the control group. One author of the paper said in an interview that the length of recall period is an important factor, with shorter recall periods being more accurate. They said, “Individuals will tend, for longer periods of recall, to describe general memories, ‘What did I do?’ in a general sense, rather than specific memories.” Stewart et al. (2024) characterize this as a “random” bias; we are not confident that recall bias is generally random but do not have a clear sense of the size or direction of this recall bias.
• Systematic self-reporting (including recall) bias influenced by social desirability: Participant communities often have positive beliefs about breastfeeding, so mothers in both control and treatment groups may tend to overreport—either intentionally or through systematic effects on self-report (including recall) accuracy—their breastfeeding intensity due to social desirability bias. However, women in the treatment group likely gain knowledge that higher intensities of breastfeeding are optimal, meaning the extent of social desirability bias may be higher than in the control group. This may cause breastfeeding intensity data for the treatment group to be systematically exaggerated.

Stewart et al. (2024) showed that there was a significant amount of bias in maternal reports of breastfeeding outcomes—including the duration of exclusive breastfeeding—in a Kenya randomized controlled trial (see our summary in Appendix B). Although strongly suggestive of bias, the paper’s results do not lend themselves to a quantitative estimate of the amount of bias in maternal reports of EBF duration, since that would require knowledge of the true EBF duration.

In the discussion section of Stewart et al. (2024, pp. 6-8), the authors discuss the use of objective biomarkers to assess true breastfeeding intensity,^[1] and review findings from past studies that have tried to validate EBF reports. The authors list mixed findings from five studies that have compared biomarker measurement of breastfeeding intensity with maternal self-report (one of which was conducted in a trial setting),^[2] showing substantial overestimation of EBF in two cases but also one case where there was a relatively good correlation between self-report and biomarker measurement. In our interview, one of the authors expressed skepticism about using the existing biomarker-based breastfeeding data to answer GiveWell’s questions, as the data tend to be from small sample sizes, only rarely from trial settings, and the extent of social desirability bias is likely to vary significantly across cultural contexts.

Our rough takeaway is that, while the likely amount of overall bias is high, it is impractical to come to a universal quantitative bias adjustment. We caution readers that the following analysis does not factor in potential bias in breastfeeding intensity data.

Our approach to answering this question

Initially, we intended to synthesize findings from a literature review of RCTs of breastfeeding promotion programs and a series of expert interviews. However, we found that very few studies both measured and reported intervention-induced changes in breastfeeding intensities other than exclusive breastfeeding rate, and we were unable to identify relevant unpublished or grey literature. Experts also did not provide us with direct answers to most of Q1, citing a lack of evidence. As a result, we took the following, two-pronged approach:

We looked into the limited available RCT evidence using an extremely rough quantitative approach, relying heavily on a small number of studies that reported data in a format amenable to analysis of movement among breastfeeding intensity categories due to intervention. As mentioned above, the approach does not attempt to adjust for biases that may arise from maternal reporting of exclusive breastfeeding.

We supplemented the quantitative approach with qualitative insights from expert interviews into the breastfeeding promotion process and how these may interact with breastfeeding intensity distributions. However, as mentioned, experts did not tend to answer the question directly, and were generally reluctant to hypothesize about likely distributional shifts induced by breastfeeding promotion in the absence of data.

Qualitative insights from expert interviews

We interviewed five experts in the field of breastfeeding and nutrition research, and reached out to several others who did not respond. Experts offered general insights into the field of breastfeeding promotion, which we group into four main themes below. More detailed discussions of each theme, along with expert quotations on the topics, can be found in Appendix C.

Theme 1: Empirical and data limitations

Experts all highlighted significant gaps in empirical data on breastfeeding intensity and the distribution changes associated with programs. Michael Kramer (a retired pediatrician and professor in McGill University’s Departments of Pediatrics and of Biostatistics and Epidemiology who has specialized in breastfeeding) noted that no additional analyses of these changes appear to exist, and relevant data are scarce. Another expert explained that breastfeeding behavior is challenging to measure accurately, as it is dynamic and influenced by bias, whereas studies typically rely on cross-sectional snapshots. This is compounded by inconsistencies in recall periods across trials, making cross-study comparisons difficult. See above for a more detailed discussion of bias.

Two of our interviews touched on potential research work to alleviate such gaps. As we discuss in a later section, Kramer informed us that it would be possible to conduct extra analysis on the Promotion of Breastfeeding Intervention Trial (PROBIT) study’s intensity data, which could allow us to better understand intensity-distributional effects in the early months post-birth. In addition, he recommended speaking with Katharina Lichtner at the Family Larsson-Rosenquist Foundation, which is specifically devoted to funding and implementing breastfeeding research. In our conversation with one of the authors of Stewart et al. (2024), we discussed the potential to develop a measure for social desirability bias in breastfeeding research (more details here), which they agreed would be valuable.

Theme 2: Breastfeeding intensity transitions over time

Thorkild Tylleskär (a pediatrician and professor at the University of Bergen’s Centre for International Health) highlighted early initiation of breastfeeding (EIBF) as the most critical intervention point. He explained that a good start can set a positive trajectory for breastfeeding, whereas a poor start often leads to early cessation. He also shared a graph of an ideal pattern of infant feeding, advocating for complementary foods at six months and family foods by nine months to ensure sufficient nutrition, which can be found in Appendix C.

Experts agreed that breastfeeding intensity tends to decline over time and reversals to more exclusive breastfeeding are rare. One expert said that once other foods or liquids are introduced, it becomes difficult for mothers to return to exclusivity. Kramer explained that partial breastfeeding is often a transition phase: “The mother’s milk supply dries up quickly,” particularly when external factors like returning to work limit breastfeeding opportunities, although some mothers can maintain partial breastfeeding at 50% or even sustain minimal “token” breastfeeding.

Theme 3: Impact pathways and barriers to breastfeeding

Experts highlighted that a mother’s decision to breastfeed is often influenced by family, community, and workplace dynamics. Kramer noted that decisions are frequently shaped by mothers’ mothers, mothers-in-law, and other relatives. Tylleskär and another expert added that cultural norms often support breastfeeding but may discourage exclusivity, with relatives urging mothers to introduce other foods early (this dynamic is further discussed in a later section).

In countries where women return to the formal workplace as early as four months after giving birth, work pressures can be a burden, while Daniele Lantagne (a research professor in Tufts University’s School of Engineering whose group looks at water, sanitation, and hygiene programs in LMIC and crisis contexts) and another expert both noted that rural women working in subsistence agriculture often have higher breastfeeding rates due to their ability to keep their infants with them at work. Tylleskär also identified the commercial formula industry as a major threat to breastfeeding. He described aggressive marketing tactics, including hospital visits by marketers in white coats and deceptive social media messaging, and emphasized the need for stronger regulation of formula marketing.

Theme 4: Disadvantages of breast milk alternatives and complements

Experts argued that breast milk alternatives and complementary foods pose significant risks to children in low-resource contexts, even beyond questions of water quality. Lantagne noted that formula supply chains are often unreliable, forcing mothers to introduce suboptimal foods when formula becomes unavailable, and that formula also carries safety risks due to bacterial growth in unfinished bottles. Complementary foods, such as gruels and porridges, are typically less calorically dense than breast milk, leading to inadequate caloric intake. Tylleskär and another expert highlighted that children consuming these foods often fail to meet their energy needs, exacerbating malnutrition risks. Multiple experts said that such risks are particularly acute for uneducated mothers and those in low-resource settings.

1a. How do breastfeeding promotion programs affect the distribution of breastfeeding intensities in a typical target population?

Rough takeaways from looking at the RCT evidence

[Some of the high-level takeaways here are summarized from content in the following section.]

In general, we expect an across-the-board increase (or up-the-chain shift) in breastfeeding intensities due to breastfeeding promotion programs (medium confidence). While there might be stronger effects on particular counterfactual intensities, we could not determine whether this is the case because we cannot observe within-category changes.

• In terms of effect on intensity category: Our rough analysis of the limited data suggests that breastfeeding promotion programs are often effective at causing significant (>20%) proportions of mothers across all non-exclusive intensity categories to switch to higher categories (low confidence). Programs might be more effective at causing mothers who would otherwise fall in relatively high—though still non-exclusive—categories of breastfeeding intensity to go up in breastfeeding intensity category.^[3]
• In terms of actual effect on underlying intensity: Since we cannot observe within-category effects, the programs do not necessarily cause the greatest change in breastfeeding intensity among a particular group. The fact that we cannot observe within-category effects is an especially significant concern for the partial breastfeeding group, which spans the widest range of possible underlying intensities.

Since we looked at two studies with very different baseline levels^[4] of breastfeeding intensity, we also considered whether baseline intensity might interact with the distributional effect of programs. Our guess is that the targeted population’s baseline intensity of breastfeeding does not have a large effect on how evenly distributed a program’s impact is among individual mothers with different counterfactual intensities (very low confidence).^[5]

Simply from looking at the data, it is not obvious whether an increase in breastfeeding intensity caused by breastfeeding promotion is more evenly distributed across counterfactual intensities (i.e., more “across-the-board”) or more concentrated among particular counterfactual intensities. One of the main studies (Kramer et al., 2001) we looked at had overall low intensities in the control group (indicating a low baseline intensity of breastfeeding), while another (Bhandari et al., 2003) had overall high intensities in the control group.^[6]

When conceptualizing breastfeeding intensity as an ordinal categorical variable, there is a “ceiling effect” associated with exclusive breastfeeding “maxing out” the scale of possible intensities. As a result, in contexts with lower baseline levels of breastfeeding (see left panel of Figure 2), the somewhat evenly distributed nature of this shift is likely to be more apparent, in terms of the relative size of each discrete category of intensity (with increases in partial, predominant, and exclusive breastfeeding, and a decrease in non-breastfeeding). For populations with overall higher baseline levels of breastfeeding (see right panel of Figure 2), the across-the-board nature of the shift is likely to appear more muted, in those terms (with increases only in exclusive breastfeeding, and decreases in partial, predominant, and non-breastfeeding).

We think that the underlying phenomenon is likely essentially similar for populations with both low and high baseline levels of breastfeeding and that this is clearer when conceptualizing breastfeeding intensity as a continuous rather than ordinal variable (Figure 2).^[7]

Figure 2: Rough sketch of breastfeeding intensity distributional shifts given different baseline intensities

Note. The graphs show sample probability density functions in populations targeted by breastfeeding promotion programs, with the left panel representing a low baseline breastfeeding intensity and the right panel a high baseline breastfeeding intensity. The horizontal axis conceptualizes breastfeeding intensities as a continuous variable, where a value of zero represents non-breastfeeding and a value of one exclusive breastfeeding.

To interrogate this possibility further, we generated cumulative ordinal models of the breastfeeding intensity outcomes reported in two studies with different baseline/control group levels of breastfeeding (see Appendix D for the full write-up). This approach models the ordinal categories as the result of a latent normal distribution, which is shifted up or down due to the breastfeeding intervention, such that the likelihood of falling into the different categories changes. One simple model supports the idea that the two trials may have seen similar effect sizes. A “category-specific” model that allows for changes in the thresholds at which responses are categorized as a result of the intervention, suggests that the study with the lower baseline saw a slightly larger general shift in the latent scale (and therefore a slightly larger overall effect size). These findings are not decisive, as we did not have access to additional information on potentially confounding variables that could also influence the effect sizes (such as recipient characteristics or location data). Overall, the exercise suggests that the two trials may have seen similar or just slightly different effect sizes, despite their different baseline levels of breastfeeding intensity. Although this lends some support to our sense that baseline level may not matter much, this comparison of two trials is mostly illustrative—we demonstrate that it is possible to have similar effect sizes in high- and low-baseline contexts, not that this should generally be expected.

Our analysis of shifts across breastfeeding intensity categories has severe limitations. Our chief concern is that the categories span differently sized ranges on the latent scale (i.e., the partial category encompasses the vast majority of the range of possible breastfeeding intensities) and that there are potentially large shifts within the partial category that the studies could not detect. Another concern is that this may obscure potentially sharp boundary effects between adjacent categories. In particular, the small difference in proportion of breast milk consumed between predominant and exclusive is hypothesized by some researchers to have a disproportionately large effect on health outcomes. In addition, there are severe data limitations due to likely recall bias and social desirability bias (see earlier discussion).

A summary of the available RCT literature on this topic

We reviewed 21 RCTs,^[8] identifying three with specific data on breastfeeding intensity that we highlight in the report text, and six more that we mention in the spreadsheet. We mainly used data from Bhandari et al. (2003) and Kramer et al. (2001), which describe breastfeeding intensity using all four categories (exclusive, predominant, partial, and none) as defined above. We also relied on Kupratakul et al. (2010) to a lesser extent, which has similarly granular data but a much smaller sample size.

We identified five RCTs—Sikander et al. (2015), Vitolo et al. (2005) [English], Vitolo et al. (2014), Rotheram-Borus et al. (2014), Morrow et al. (1999), and Haider et al. (2000)—that only report data for three categories (exclusive, predominant or partial, and none), but we did not use them in the following analysis because the data did not seem sufficiently granular for the purposes of looking at distributional effects. After our initial review of papers, we looked more closely at study protocols to see whether authors might have collected intensity data but not reported it and found that this may have been the case for several studies (Table 4).

A note on language in the following subsections

Below, we discuss RCTs in which a treatment group receives breastfeeding promotion while a control group does not. For both groups, these trials report the proportion of mothers who fall into different breastfeeding intensity categories: exclusive, predominant, partial, and none. The studies do not show individual mothers changing their behavior as a result of breastfeeding promotion.

However, comparing the treatment and control groups, we see differences in the relative size of the categories, allowing us to infer movement among the categories (which we call “categorical flows” that can be analyzed in terms of “inflows” and “outflows”) given two assumptions: 1) randomization was successful; 2) interventions only had neutral-to-positive effects.

Therefore, in the subsequent subsections, we use simplistic and intuitive phrases such as “predominant-to-exclusive flows,” “[mothers] changed their behavior to increase intensity,” and “counterfactually predominantly breastfeeding mothers” when discussing the results of experimental trials. When we describe mothers as changing their behavior in response to intervention, the actual behavior change being described can be thought of as delaying the reduction in breastfeeding intensity due to intervention^[9] rather than increasing breastfeeding intensity due to intervention.^[10]

Bhandari et al. (2003): RCT in India, 1998-2002

Bhandari et al. (2003) studied the effects of a community-based educational intervention to promote exclusive breastfeeding until six months postpartum. The research took place between 1998 and 2002 in Haryana State, Northern India, enrolling 1,115 mother-infant dyads from communities located 3-5 km from the state’s main highway. At three months postpartum, the investigators collected data on breastfeeding intensity, using the four categories (exclusive, predominant, partial, and none) as reported through “24 h dietary recall,”^[11] which was elicited by trained nutritionists (p. 1419).^[12] They do not appear to have collected non-exclusive breastfeeding rates at other follow-up periods.

Their results (Table 1, Figure 3) show strong effects on exclusive breastfeeding intensity at three months postpartum. The categorical data indicate that the exclusive breastfeeding rate increased (by 31.1 percentage points), while predominant, partial, and non-breastfeeding rates decreased (by 20.8, 9.1, and 1.2 percentage points, respectively) in the treatment group relative to the control group. This finding is consistent with very significant predominant-to-exclusive flows and non-negligible partial-to-exclusive and/or none-to-exclusive flows. In other words, the effects appear to be concentrated at the top of the chain, at least when data are viewed categorically, at three months postpartum.

Table 1: Effects of a breastfeeding promotion program in India, 3 months postpartum

Note. Summary of Bhandari et al. (2003) results; adapted from Table 2, p. 1421.

Figure 3: Bhandari et al. (2003) results as stacked bar charts

Note. Summary of Bhandari et al. (2003) results.

A deeper analysis of the results reinforces the observation that, as a proportion of the control group, counterfactually predominantly breastfeeding mothers saw the largest increase in intensity level as a category. However, there were still across-the-board effects on intensity, with more than 40% of mother-infant dyads “moving up the chain” from each non-exclusive category. Looking at increases in breastfeeding intensity by category, and assuming the program only had neutral- to-positive effects on individual mothers’ breastfeeding intensity levels:^[13]

• 41% of non-breastfeeders moved up in breastfeeding intensity category: Among the very small proportion (2.9%) of non-breastfeeding mothers, 41% (1.2 percentage points) changed their behavior to increase intensity due to the program, i.e., this is the gross (and net) outflow from this category. It’s unclear which intensity levels they switched to, with options ranging from partial to exclusive.
• 41%-47% of partial breastfeeders moved up in breastfeeding intensity category: The partial breastfeeding category saw a gross outflow of at least 9.1 percentage points (assuming zero inflow from non-breastfeeding) and at most 10.3 percentage points (assuming maximal inflow from non-breastfeeding) to the predominant and exclusive categories. Thus, between 41% and 47% of partially breastfeeding mothers changed their behavior to increase intensity under this assumption.

• 76%-100% of predominant breastfeeders moved up in breastfeeding intensity category: Under this assumption, the predominant breastfeeding category saw a gross outflow of at least 20.8 percentage points (assuming zero inflow from lower intensities) and at most 27.2 percentage points (assuming inflows from lower intensities were just enough to replenish outflows from predominant)^[14] to the exclusive category. Thus, between 76% and 100% of predominantly breastfeeding mothers changed their behavior to increase intensity under this assumption.

Looking at gross inflows by category, with the same assumption that the program had neutral-to-positive effects, we think that the inflows to higher categories of breastfeeding intensity are likely to originate mostly from the next-lowest category. However, this is only obvious from the data for inflows to exclusive; the source of inflows to predominant is unclear and, by our assumption, inflows to partial can only come from non-breastfeeders.

• The composition of the gross (and net) inflow to the exclusive category (31.1 percentage points) can take the following configurations, all of which suggest the bulk of the growth in exclusive breastfeeding is explained by behavior change among predominantly breastfeeding mothers:

• • Inflow from predominant breastfeeding: between 20.8 percentage points and 27.2 percentage points (see here), or 67% to 87% of the gross/net inflow
  • Inflows from partial and non-breastfeeding: it follows (from the previous bullet) that 13% to 33% of the gross/net inflow must come from these two categories
    • Specific inflow from partial breastfeeding: between 3.9 percentage points^[15] and 10.3 percentage points, or 13% to 33% of the gross/net inflow^[16]
    • Specific inflow from non-breastfeeding: ≤1.2 percentage points, or ≤4% of the gross/net inflow
• The gross inflow to the predominant category from lower intensities can range from zero to 6.4 percentage points (zero to 100% of the gross inflow). It is zero if flows from lower intensities go exclusively to other categories instead, and it is 6.4 percentage points if 100% of predominant (at control) flows out to exclusive.
  • Specific inflow from partial breastfeeding: ≤6.4 percentage points, or ≤100% of the gross inflow
  • Specific inflow from non-breastfeeding: ≤1.2 percentage points, or ≤19% to ≤100% of the gross inflow (depending on the size of the gross inflow)
• The gross inflow to the partial category from none can range from zero to 1.2 percentage points (zero to 100% of the gross inflow). It is zero if flows from none go exclusively to predominant or exclusive, and it is 1.2 percentage points if flows from none go exclusively to partial.

Kramer et al. (2001): RCT in Belarus, 1996-1997

Kramer et al. (2001) studied the effects of a hospital-based intervention modeled after UNICEF’s Baby-Friendly Hospital Initiative, which involves breastfeeding promotion in an RCT called the “Promotion of Breastfeeding Intervention Trial (PROBIT).” The trial took place between 1996 and 1997 across 34 maternal hospitals and associated polyclinics^[17] in urban and rural regions throughout Belarus, with one-year follow-up, and enrolled 17,046 mother-infant dyads.^[18] The investigators recorded breastfeeding intensity categorical data “[c]onsistent with WHO definitions … at all visits up to and including the 3- and 6-month visits” (p. 415). Kramer confirmed that infant feeding data collection took place at one, two, three, six, nine, and 12 months postpartum.^[19]

From this context, we inferred that there might be unpublished results on breastfeeding intensity at one, two, nine, and/or 12 months postpartum. Kramer said that while the results were never computed, the raw data needed to produce them do exist. He said that Emily Oken’s group at Harvard have access to the data, and suggested they would likely be able to conduct the analyses. We did not independently confirm this with Oken. We think that commissioning these analyses could be of interest to GiveWell, conditional on GiveWell’s continued interest in answering the brief’s questions. We would primarily be interested in seeing the data for one month and two months postpartum to better understand the distributional effects of breastfeeding promotion in the early months.

The investigators collected data (including on breastfeeding intensity) through both polyclinic charts and maternal interviews for a subset of participants as a “routine audit of data validity” because the pediatricians charged with observing clinical outcomes were also involved in program implementation, and therefore could not be blinded to the study infants’ treatment group assignment (pp. 415-416).^[20] This indicates that data used in analyses were from pediatricians’ polyclinic charts, and thus were elicited by pediatricians at polyclinic visits. While the paper does not describe the elicitation method, nor the relevant feeding period (e.g., in the case of Bhandari et al., 2003, the past 24 hours), Kramer said that the pediatricians recorded feeding behavior over the whole postnatal period (i.e., from birth to the first follow-up and since the previous follow-up at each subsequent follow-up). We do not think that this has major implications for data interpretation (in terms of, e.g., comparison with Bhandari et al., 2003), because this change would affect both control and treatment groups, though we acknowledge that the comparison is imperfect due to different elicitation methods and recall periods.

The definitions of breastfeeding intensity categories, as reported in the paper’s results section, were also not immediately clear to us. In a previous draft, we represented the categories as discrete. After our conversation with Kramer, we updated our discussion to reflect the paper’s schema—that the size of a given intensity category reported by the authors includes all mother-infant dyads at or above that intensity category.^[21]

Compared to those of Bhandari et al. (2003), the results of PROBIT (Table 2, Figure 5) show even more clearly that breastfeeding promotion induced large across-the-board increases in breastfeeding intensity, at both three months and six months postpartum. At three months postpartum, the categorical data show that the exclusive breastfeeding rate increased (by 36.9 percentage points), while predominant, partial, and non-breastfeeding rates decreased (by 13.3, 10.9, and 12.7 percentage points, respectively), consistent with significant predominant-to-exclusive flows and significant partial-to-exclusive and/or none-to-exclusive flows. The latter flows must also be significant because—assuming the program had neutral-to-positive effects on breastfeeding intensity—even if 100% of predominant flowed out to exclusive, that would explain just 59% of the inflow to exclusive.^[22] In other words, compared to Bhandari, the effects appear to be somewhat less concentrated at the top of the chain at three months postpartum, when data are viewed categorically.

We considered and rejected several plausible explanations for this difference. One possibility that stood out was that the overall effect size of PROBIT is simply uniformly larger than in the Bhandari study, enabling the mothers in the lowest-intensity categories to more successfully “leapfrog” the intermediate categories. Another was that the PROBIT intervention is more effective on lower-intensity participants than the Bhandari study’s intervention. Neither possibility appears true, however, when comparing the persuasion rates of the intervention for mothers in non-exclusive breastfeeding categories (see here and here)—in fact, the Bhandari study seemed to have higher persuasion rates, and the studies seem similar even in their effectiveness across categories.^[23] Independent of relative intervention effectiveness, we think it matters that the target population in PROBIT starts with lower overall breastfeeding rates (40% vs. 3% non-breastfeeding), and believe that this could cause categorical flows to appear more conspicuously “across-the-board” in PROBIT for reasons outlined earlier.

Table 2: Effects of a breastfeeding promotion program in Belarus, 3-12 months postpartum

Note. Summary of Kramer et al. (2001) results; see also p. 417 of the paper.

Figure 4: Kramer et al. (2001) results as stacked bar charts

Note. Summary of Kramer et al. (2001) results.

Looking at gross outflows by category, and assuming the program only had neutral-to-positive effects on individual mothers’ breastfeeding intensity levels, we find generally similar (but slightly lower) rates of movement across intensity categories as in the Bhandari study, with more than 30% of mother-infant dyads moving up the chain from each non-exclusive category and with the strongest persuasion effects seen in mothers who, counterfactually, would have predominantly breastfed:

• 32% of non-breastfeeders moved up in breastfeeding intensity category: None saw a gross/net outflow of 12.7 percentage points, meaning 32% of mothers changed their behavior to increase breastfeeding intensity due to the program.
• 34%-74% of partial breastfeeders moved up in breastfeeding intensity category: Partial saw a gross outflow of at least 10.9 percentage points (assuming zero inflow from non-breastfeeding) and at most 23.6 percentage points (assuming maximal inflow from non-breastfeeding) to the predominant and exclusive categories. Thus, between 34% and 74% of partially breastfeeding mothers changed their behavior to increase intensity under this assumption.
• 61%-100% of predominant breastfeeders moved up in breastfeeding intensity category: Predominant saw a gross outflow of at least 13.3 percentage points (assuming zero inflow from lower intensities) and at most 21.9 percentage points (assuming inflows from lower intensities were just enough to replenish outflows from predominant)^[24] to the exclusive category. Thus, between 61% and 100% of predominantly breastfeeding mothers changed their behavior to increase intensity under this assumption.

Looking at gross inflows by category, with the same assumption that program had neutral-to-positive effects, we find that there is generally a more even mix of flows into the exclusive category from lower categories than in the Bhandari study and that it is even plausible (though not necessarily likely) that partial-to-exclusive flows might exceed predominant-to-exclusive flows:

• The composition of the gross/net inflow to exclusive (36.9 percentage points) can take the following configurations:
  • Inflow from predominant breastfeeding: between 13.3 percentage points and 21.9 percentage points (see here), or 36% to 59% of the gross/net inflow
  • Inflows from partial and non-breastfeeding: it follows that 31% to 64% of the gross/net inflow must come from these two categories.
    • Specific inflow from partial breastfeeding: between 2.3 percentage points^[25] and 23.6 percentage points, or 6% to 64% of the gross/net inflow^[26]
    • Specific inflow from non-breastfeeding: ≤12.7 percentage points, or ≤34% of the gross/net inflow
• The gross inflow to predominant from lower intensities can range from zero (if flows from lower intensities go exclusively to other categories instead) to 8.6 percentage points (if 100% of predominant flows out to exclusive). It’s not possible to bound the specific proportion of inflows from partial and none.
• The gross inflow to partial from none can range from zero (if flows from none go exclusively to predominant or exclusive) to 12.7 percentage points (if flows from none go exclusively to partial).

At six months postpartum (where the Bhandari study is no longer as relevant a comparator), the categorical data continue to show an increase in the exclusive breastfeeding rate (by 7.3 percentage points) due to intervention. Unlike at three months, however, categories other than non-breastfeeding also grow in size—predominant by 1.7 percentage points and partial by 4.7 percentage points—while non-breastfeeding decreases by 13.7 percentage points, due to intervention. The effects at this later observation appear more evenly spread across categories, likely in part because of the general decline in breastfeeding rate as the infant grows further, alleviating the ceiling effect (as outlined earlier). We discuss the relevance of this observation further in Q1b later.

Looking at gross outflows by category, and assuming the program only had neutral-to-positive effects on individual mothers’ breastfeeding intensity levels at six months, we find an overall significantly lower rate of movement across intensity categories compared to three months postpartum, although there could have been an extremely large proportional movement from predominant to exclusive:

• 21% of non-breastfeeders moved up in breastfeeding intensity category: “None” saw a gross/net outflow of 13.7 percentage points, meaning 21% of mothers changed their behavior in response to the program.
• ≤26% of partial breastfeeders moved up in breastfeeding intensity category: “Partial” saw a net inflow in this case, so the lower bound on the proportion that moved up is zero. Assuming maximal outflows from partial to higher intensities, 9.0 percentage points could have moved up (making up all of the difference between treatment and control in higher categories), meaning 26% of partially breastfeeding mothers changed their behavior to increase intensity due to the program.
• An unknown proportion of predominant breastfeeders moved up in breastfeeding intensity category: “Predominant” saw a net inflow in this case, so it’s not possible to set a lower bound, while the maximal outflow represents the entirety of the group (1.0 percentage points). Thus, the true proportion could be anywhere between zero and 100%.

Looking at gross inflows by category, assuming that program had neutral-to-positive effects, we find that the inflow from partial and none to exclusive (≥86%) makes up a significantly larger proportion at six months than at three months (31%-64%). This indicates that, in the Kramer trial, while it was overall less likely that a low (partial/none) breastfeeding intensity would be changed at six months compared to three months postpartum, among women who did change their intensity to exclusive breastfeeding, low rates of counterfactual breastfeeding made up a bigger proportion at six months compared to three months (see more here). Other inflows couldn’t be determined.

• The composition of the gross/net inflow to exclusive (7.3 percentage points) can take the following configurations:
  • Inflow from predominant breastfeeding: between zero and 1.0 percentage points, or ≤14% of the gross/net inflow
  • Inflows from partial and non-breastfeeding: it follows that ≥86% of the gross/net inflow must come from these two categories, though it’s not possible to determine specific inflows.^[27]
• The gross inflow to predominant from lower intensities can range from zero (if flows from lower intensities go exclusively to other categories instead) to 2.7 percentage points (if 100% of predominant flows out to exclusive). It’s not possible to determine specific inflows from partial and none.
• The gross inflow to partial from none can range from 4.7 percentage points (the net inflow) to 12.7 percentage points (if flows from none go exclusively to partial).

Kramer implied that the intensity of treatment (how strongly pediatricians were encouraging exclusive breastfeeding) may have decreased around the four-month mark in the trial due to contemporaneous advice from the WHO, which was then recommending four to six months of exclusive breastfeeding. This may have contributed to a smaller effect size at six months in PROBIT than what one would expect in a trial today.

Kupratakul et al. (2010): RCT in Thailand, 2009

Krupatakul et al. (2010) studied the effects of a hospital-based educational intervention to promote exclusive breastfeeding until six months postpartum. The research took place in 2009 and enrolled 80 mother-infant dyads from two hospitals in Bangkok. The study had an extremely small sample size, and we therefore have even lower confidence in its outcomes compared to Bhandari et al. (2003) and Kramer et al. (2001). We still include a brief write-up on the study because it recorded unusually granular breastfeeding intensity outcome data. The investigators collected data on breastfeeding intensity at seven days, 14 days, and one month postpartum, then monthly until six months, using the four categories (exclusive, predominant, partial, and none) as reported through telephone interviews^[28] (p. 1011).

Their results (Table 3, Figure 6) show strong effects on exclusive breastfeeding over the six-month postnatal period for which there are data. The categories are remarkably evenly sized throughout the data collection period and are consistent with a relatively even movement up the chain of intensity levels, though with more of the movement coming from the none category as time progresses. The discontinuation rate of exclusive breastfeeding over time seems roughly linear in the treatment group, whereas there is a sharp cliff after three months in the control group.

Table 3: Effects of a breastfeeding promotion program in Thailand, 1-6 months postpartum

Note. Summary of Kupratakul et al. (2010) results; adapted from Table 5, p. 1016. Data for seven days and 14 days postpartum omitted from adapted table.

Figure 6: Kupratakul et al. (2010) results as stacked bar charts

Note. Summary of Kupratakul et al. (2010) results.

Other experimental and observational trials

In addition to the three trials discussed above, we identified five studies that reported just three breastfeeding intensity categories, in effect combining the predominant and partial categories, as summarized in this spreadsheet. (We only partially completed the spreadsheet. A previous draft reported some of the results of these five studies, but we deprioritized looking into them due to insufficient granularity.) We reviewed a total of 21 studies sourced from GiveWell’s CEA meta-analysis, McFadden et al. (2017) via GiveWell (2018), and Olufunlayo et al. (2019).

To determine whether studies did not assess the relevant intensity outcomes, or if they (likely) assessed but did not report those outcomes, we checked each study’s protocol/methodology section. In Table 4, we show that several studies likely assessed but did not report partial breastfeeding intensity measurements, although it was overall challenging to determine conclusively whether a study assessed partial breastfeeding intensity given the vague language used in methodological write-ups (see examples in Table 4 footnotes).

Table 4: Protocols of relevant RCTs on the effects of breastfeeding promotion

Note. *More longitudinal data were likely collected. ^†The data were likely collected but only fragments were reported (insufficient to reconstruct fully the intensities at a single point in time).

1b. Is there any evidence for these impacts on different child age cohorts?

What we can tell from the limited RCT evidence

In the prior section, we discussed two studies that display program effects at different stages postpartum. The studies—Kramer et al. (2001) and Kupratakul et al. (2010)—offer some insights into the effects of breastfeeding promotion programs across intervention designs and infant age cohorts. The studies from which we pull evidence ran programs that continued promotion as children aged until the months where breastfeeding intensity and diarrheal outcomes are measured, rather than just targeting parents shortly before/after birth.

Our overall impression from the limited RCT literature, and the below summary of other evidence, is that breastfeeding promotion likely causes across-the-board increases in breastfeeding intensity that persist as the infant grows (low confidence). The composition of flows among intensity categories also appears to change over the first six months of infant life in two ways:

• As the infant ages, mothers with lower counterfactual breastfeeding intensities become less likely to respond to intervention by going up in breastfeeding intensity category (very low confidence).

• As the infant ages, among mothers who respond to intervention by switching to exclusive breastfeeding, an increased share do so from the lowest counterfactual intensities (none, partial). This seems to mostly be a composition effect since the proportion of predominant breastfeeders shrinks rapidly in the control group (very low confidence).

These changes are consistent with the observation that breastfeeding intensities generally—and exclusive breastfeeding rates in particular—decrease during an infant’s early months, alleviating the ceiling effect (as outlined here) and making the effect of programs appear more noticeable toward the middle of the intensity ladder (though this does not necessarily mean that the program effects on intensity are more evenly distributed across counterfactual intensities). These decreasing intensities are likely due to a combination of diminishing program effectiveness, reduced contact with interventions over time, the generally increased likelihood of breastfeeding cessation as time passes, and diminishing intensity of intervention.^[42] Experts mentioned factors such as needing to return to work and diminishing social pressure to breastfeed at high intensities (or conversely, increasing social pressure to cease breastfeeding). This drop in social pressure makes sense, as our brief overview of the literature does indicate that breastfeeding’s health-related impacts likely decrease after the six-month mark.

To supplement this limited picture from the RCT evidence, we expanded our research to evaluate other evidence of breastfeeding promotion and its impact across intensities at various stages postpartum, as well as the evidence of the health effects of various levels of breastfeeding intensity on children at different developmental stages.

Program impacts on breastfeeding practices at various ages

Early initiation of breastfeeding (EIBF), defined as putting the infant to the breast within one hour of birth, has been a key focus of some breastfeeding promotion programs. EIBF does not necessarily imply exclusive breastfeeding, but nonetheless confers extensive benefits, as discussed in the following section.

Sinha et al. (2015) found that home- and community-based counseling or educational interventions led to an 85% increase in EIBF rates, identifying this strategy as the highest priority intervention for early breastfeeding behaviors (in a systematic review/meta-analysis, p. 122). Similarly, Lassi et al. (2020), in a systematic review of breastfeeding education interventions in LMICs, reported a 20% increase in EIBF rates (p. 8). Khatib et al. (2023), in an overview of systematic reviews in low-income countries (LICs) and LMICs, highlighted that Community-Based Intervention Packages (CBIP) delivered by trained nurse-midwives increased EIBF rates significantly (relative risk [RR] = 1.93). Peer counseling and educational interventions also improved EIBF rates, albeit with varying effectiveness depending on the context and personnel involved (RR = 1.44–1.70, p. 8).

Breastfeeding promotion programs also show robust effects on breastfeeding behavior in mothers of infants older than a few hours but under six months. Lassi et al. (2020) found that breastfeeding education interventions in LMICs led to a dramatic 102% increase in EBF rates at three months and a 53% increase at six months (p. 8 and 13, respectively). Similarly, Dib et al. (2023) reported a significant improvement in EBF rates up to six months (OR = 3.15, abstract, meta-analysis of RCTs).

Susiloretni et al. (2019, in a prospective cohort study in Indonesia, offered a potential cautionary note when they found no direct link between EBF and longer breastfeeding duration. Instead, behavioral factors such as maternal beliefs and confidence were more predictive of sustained breastfeeding. Interestingly, exposure to EBF promotion was identified as a risk factor for shorter breastfeeding duration (HR = 4.09, from abstract), suggesting that poorly tailored messaging or program designs could inadvertently undermine long-term breastfeeding goals.

Programs aimed at extending the duration of breastfeeding past the six-month mark (also known as “continued breastfeeding” or “continuance” or “continuation,” usually taken to mean breastfeeding with complementary foods rather than EBF) have also had somewhat mixed results. Van Dellen et al. (2019) reported that breastfeeding support programs in the Netherlands reduced the risk of discontinuing EBF by 54% at six months (abstract). Gavine et al. (2022), in a Cochrane review, found that breastfeeding-only support interventions were associated with a 10% reduction in EBF cessation at six months (RR = 0.90), while integrated “breastfeeding-plus” programs, which combined breastfeeding support with broader maternal and child health interventions, achieved a more substantial 21% reduction (RR = 0.79). In addition, Sinha et al. (2015) found that educational interventions delivered across both health systems and homes were the most effective for improving continued breastfeeding rates^[43], with a 34% increase reported (p. 123, in a systematic review of studies in a range of contexts).

Health impacts of breastfeeding at various stages postpartum

In this section, we discuss the available evidence concerning the impacts of initiating and continuing breastfeeding across various infant ages, from the first few hours to the one-year mark and beyond. For a more comprehensive discussion of health benefits across breastfeeding intensity levels, please refer to the later section.

In our conversation, Tylleskär emphasized the importance of EIBF repeatedly, primarily for its impact on lactation and habit formation. He noted that breastfeeding behaviors have some path dependency, and emphasized that setting the trajectory of breastfeeding early can significantly influence intensity and duration. He also highlighted the critical role of EIBF in early immunity, describing breast milk as both a “food and vaccine” specifically protective of the infant in their likely environment. He said that while “the food part of [breast milk] can be replaced, the vaccine part of it cannot be replaced easily. A mother that grows up in a particular place will develop antibodies against pathogens that she has encountered in that environment.”

Engelhart et al. (2022), in a systematic review of RCTs, emphasized the importance of EIBF, with groups receiving EIBF-promoting interventions exhibiting a 54-52% reduction in neonatal mortality compared to controls (p. 7-9). This aligns with findings from Horta (2019), who emphasized that breastfeeding’s protective effects against diarrhea and respiratory infections are most pronounced in early infancy (p. 1, in a summary of studies from around the world). Penugonda et al. (2022) also highlighted the benefits of EBF at this age, reporting significantly lower odds of illness at 10–14 weeks (OR = 0.27) and 18–22 weeks compared to non-EBF (OR = 0.50, from abstract).

The health benefits of breastfeeding for infants under six months are well-documented, although most programs appear to primarily focus on promoting EBF during the first six months, and many studies report simply “significant” effects rather than quantitative estimates. In our conversation, Lantagne noted that children start to crawl at six months, and their newfound mobility makes it more difficult to control their exposure to various environmental hazards and pathogens. Tylleskär stated that the earlier months have a much larger effect on infant health than the later ones, and estimated that breastfeeding at month two is about five times as valuable as month 12. He hypothesized that the health value of breastfeeding falls after month two, first gently, then at an increasing rate. In a meta-analysis of 32 EBF promotion studies, Dib et al. (2023) reported a 59% reduction in respiratory illness odds at 0–3 months (OR = 0.41) for exclusively breastfed infants, though effects on diarrhea were only borderline significant (OR = 0.84, 95% CI: 0.70–1.00).

Sharma and Gupta (2022) observed in a review of the general pediatric literature that breastfeeding showed immunological benefits and reduced infection risks beyond six months, although they found that the evidence for other sustained health impacts, such as growth and obesity, was mixed. Similarly, in a systematic review and meta-analysis, Hoang et al. (2021) found that EBF for at least six months significantly decreased the risk of allergic rhinitis in children (abstract). Dharod et al. (2023) found that American infants breastfed for more than six months had significantly lower growth trajectories and reduced risk of rapid weight gain compared to those breastfed for shorter periods (RR = 1.68). However, at least one study has found that prolonged breastfeeding may have diarrhea-related risks or at least correlates: Ogbo et al. (2017), in a survey study in sub-Saharan Africa, found that continued breastfeeding at one year (OR = 1.27; 95%CI: 1.05–1.55) was significantly associated with a higher risk of diarrhea (compared with no breastfeeding).

For babies breastfed beyond 12 months, the evidence of health benefits is much less plentiful and definitive. In low-income and emergency contexts, Tylleskär pointed out that continued breastfeeding can offer a mother the option to feed her child in crisis situations such as wars and famines, whereas the option is removed if she has ceased breastfeeding. Lackey et al. (2021) documented continued breastfeeding’s nutritional and immunological benefits, as well as associations with reduced infant mortality and improved birth spacing for mothers in undernourished populations (p. 285). Hadi et al. (2021), in a survey analysis, found that exclusively breastfed children under two years from poorer households were 20% less likely to be stunted compared to their non-exclusively breastfed peers (p. 7). Li et al. (2019) similarly reported that continued breastfeeding between 6-18 months in rural China reduced diarrhea and cough in children, showing benefits across intensity levels (p. 9, results in Table 6). However, Issa et al. (2019) pointed out that while longer breastfeeding durations were associated with fewer pediatrician visits and lower rates of colic, urinary tract infections, and asthma, the evidence for other outcomes such as maternal weight loss or growth trajectories was unclear.

1c. Is there any evidence or indication that these impacts differ across geographies with different baseline rates of breastfeeding intensity or cultural attitudes toward breastfeeding?

The most detailed and high-quality evidence regarding breastfeeding intensities is discussed at length in previous sections. We found very little high-quality, directly relevant RCT evidence to specifically address how breastfeeding-program impacts vary across geographies with different baseline rates of breastfeeding intensity or cultural attitudes.

Given the lack of studies in geographical contexts relevant to GiveWell, we take a different approach in the review below. Rather than providing causal insights, we then draw on broader observational studies, systematic reviews, and indirect evidence to explore regional disparities in breastfeeding practices and potential mechanisms driving these differences. While this evidence is primarily background and motivation rather than a direct answer to the question, we hope that it helps frame the issue and identify key gaps in the literature, as well as areas for future investigation.

Geographical disparities in program outcomes

In the prior sections, we discussed the few relevant high-quality studies that display detailed intensity-specific program effects at different locations. We discussed how these studies, Kramer et al. (2001) in Belarus, Morrow et al. (1999) in Mexico, and Bonuck et al. (2014) and Ahmed et al. (2016) both in New York, evaluated program effects in a specific context, and we point again to Table 2 and Table 4, as well as Figure 1. Programs in Belarus and Mexico achieved higher gains in EBF intensity compared to interventions in US contexts. We argue that the US study’s more modest impacts across the spectrum of breastfeeding practices may potentially reflect baseline cultural differences and systemic barriers. However, as previously discussed, it is notable that very few studies exist that give more insight into breastfeeding intensity changes from interventions in truly low-income countries: evidence generally is restricted to reporting EBF changes, and is concentrated in contexts other than low-income countries.

Several studies demonstrate that the same program can have widely divergent effects depending on local conditions. For example, Flax et al. (2022) reported that the Alive & Thrive program in Nigeria revealed stark contrasts between Kaduna and Lagos, two regions with different baseline readiness and implementation environments. In the study, Kaduna achieved an 8.9 percentage point increase in EBF and significant gains in early initiation and later dietary diversity. In contrast, Lagos saw no impacts.

Geographic differences in breastfeeding promotion often stem from systemic challenges and policy environments. Hernández-Cordero et al. (2022) emphasized the importance of factors like multisectoral political will, adequate financing, and evidence-based advocacy for successful program scale-up. Their comparative case study analysis of programs in Burkina Faso, the Philippines, Mexico, and the USA found that systemic barriers, such as inadequate maternity leave policies and the aggressive marketing of breastmilk substitutes, were universal challenges (p. 20).

Intervention design is also crucial; the role of antenatal and postnatal care integration in improving outcomes was emphasized in a review by Olufunlayo et al. (2019, p. 15). Kinshella et al. (2021) highlighted gaps in implementation readiness, noting that the effectiveness of facility-based breastfeeding policies in sub-Saharan Africa often depended on caregiver attitudes and local health system capacity. They argued that even well-designed programs may falter without sufficient buy-in from healthcare providers and adequate infrastructure (p. 6). These findings align with the successes in Kaduna state above highlighted in Flax et al. (2022), showing that programs spanning both phases of care often achieve greater success in shifting breastfeeding behaviors. By contrast, areas like Lagos, where such integration was likely weaker, struggled to replicate these outcomes.

Geographical baseline disparities and general trends

Global prevalence of EBF for infants under six months was 43.5% in 2019, with substantial variation across regions (Gardner & Kassebaum, 2020, systematic review, abstract).^[44] Sub-Saharan Africa generally remains below the WHO target of 50% EBF, with dramatic disparities even within the region. In Chad and Nigeria, less than 20% of infants 0–5 months were exclusively breastfed in 2019. In contrast, in Rwanda and Zambia, rates exceeded 70% (Gebremedhin 2019, cross-sectional study, p. 6). Urban-rural divides are also notable: rural women in sub-Saharan Africa breastfed more than their urban counterparts (Caldwell et al., 2023, DHS survey analysis, abstract). We are aware of several potentially useful sources to better understand breastfeeding baseline data, including DHS and WHO. While Tylleskär said that the data are generally “trustworthy,” we would caution against over-indexing on the available data, which are likely subject to significant bias. Importantly, the extent of bias may differ by geographic region. In a follow-up email, Tylleskär also highlighted that these data report a single rate for the first six months, although what is most important is the rate of breastfeeding in the first two months.

Subnational geospatial data further highlight disparities within countries. Even within countries, specific regions with lower baseline EBF prevalence are less likely to meet WHO targets without targeted interventions (Bhattacharjee et al., 2019^[45], geospatial study, p. 2-5). In addition, regions with entrenched barriers, such as food insecurity or employment-related challenges, often see EBF as a “last resort” rather than a choice, as observed in urban Haiti (Lesorogol et al., 2018, RCT, p. 6).

Rates of EIBF also vary widely. In sub-Saharan Africa, 50.5% of infants were put to the breast within an hour, with rates exceeding two-thirds in countries like Ethiopia and Rwanda but falling below 25% in Congo Republic and Chad (Gebremedhin, 2019, p. 6). Globally, early initiation has improved over the years, rising from 32% in the early 1990s to 55% between 2016 and 2020, (Hamer et al., 2022, review, p. 1).

Duration is also a key concern for infant health. While EBF rates often decline with infant age, the pattern is geographically variable. In sub-Saharan Africa, EBF rates drop from 59.5% among infants 0–1 month to 23.9% at 4–5 months (Gebremedhin, 2019, p. 6). In rural China, breastfeeding prevalence plummets from 58.2% at 6–12 months to just 5.2% at 18–24 months (Li et al., 2019, p. 5). This decline underscores the influence of socioeconomic factors and access to breastmilk substitutes, particularly in urban and wealthier settings (Neves et al., 2020, cross-sectional study, p. 685).

Sub-Saharan Africa exhibits stark disparities in EBF rates, with certain regions demonstrating significant opportunities for targeted support. Countries like Chad, Nigeria, and Gabon report EBF rates below 20% among infants aged 0–5 months, highlighting the urgent need for intervention (Gebremedhin, 2019, cross-sectional study, p. 6). Subnational geospatial analyses reveal that regions within these countries with particularly low baseline rates lag in meeting WHO breastfeeding targets (Bhattacharjee et al., 2019, p. 2-5). Targeted interventions, including culturally tailored counseling and peer support, could have high impacts in these areas, especially when combined with strategies to address food insecurity and employment challenges, as demonstrated in similar contexts like urban Haiti (Lesorogol et al., 2018, p. 6).

Cultural and sociodemographic determinants of breastfeeding baselines

Community norms, including the general acceptance of and exposure to breastfeeding, can influence the social desirability of higher-intensity breastfeeding and breastfeeding rates. One expert drew a distinction between acceptance of any breastfeeding and that of exclusive breastfeeding. In addition, traditional practices influence a variety of breastfeeding behaviors. Brown (2018) describes several examples:

• Some religious customs involve women delaying breastfeeding until a certain event or number of days. For example, “Some Hindu medical literature suggests that breastfeeding should not be started until the third day,” while “In rural Ghana, first-time mothers must go through a cultural cleansing process before they can breastfeed” (p. 152). Depending on the strength of these beliefs and customs, mothers may be more or less receptive to breastfeeding promotion, and as Tylleskär noted, delaying initiation can also impact a mother’s experience and capacity to breastfeed later on.
• Some cultures advocate giving prelacteal feeds to infants, given “perceptions that infants are born hungry and need immediate feeding.” According to Brown, “pre-lacteal feeds are common in many African, Indian, and South East Asian regions” with estimates of ~60% in Nigeria and 27% in Nepal (p. 152). Prelacteal feeds are also given as part of religious ceremonies in Hinduism (p. 152). Newborns who are given prelacteal feeds experience a delay in breastfeeding and are, by definition, not exclusively breastfed.
• Times where it is considered appropriate to breastfeed can vary. In some cultures breastfeeding in public is taboo due to concerns about the “evil eye”—“a malevolent gaze, which passes on a witchcraft curse and leads to milk drying up or breast sores.” Others believe that a “cleansing ritual” is required before a mother can breastfeed following an argument with her husband or family (p. 152). Cultures with greater restrictions on the appropriateness of breastfeeding may inhibit breastfeeding intensity.

Maternal education can influence early initiation. An observational study reported that mothers with primary education were 1.29 times more likely to practice early initiation compared to those with no formal education (Wako et al., 2022, survey analysis). However, higher education levels sometimes correlate with reduced EBF rates, as wealthier and more educated mothers may have access to breast milk substitutes and return to work earlier (Gebremedhin, 2019, p. 6; Caldwell et al., 2023, abstract).

Maternal occupation can influence breastfeeding cessation. As discussed earlier, experts mentioned that workplace social support and maternal occupation can influence the ease with which mothers who intend to breastfeed can actually do so, and thus breastfeeding intensity.

The baseline social desirability of breastfeeding likely varies by context. We learned from one expert that Rafael Perez-Escamilla (Yale School of Public Health) would be a good expert to speak with about geographical and cultural variations in the social desirability of breastfeeding, although we did not have time to do so in this project.

2. How does infant mortality differ across breastfeeding intensity levels?

Discussion of GiveWell’s mortality modeling

GiveWell follows its general mortality modeling for water quality interventions to estimate mortality and morbidity effects of breastfeeding promotion. For direct, i.e., non-digital, delivery of intervention, GiveWell uses its own meta-analysis to estimate a 16% and 11% reduction in post-neonatal and neonatal diarrhea morbidity, respectively. From GiveWell’s assumption that “BP could plausibly directly or indirectly affect 45% of neonatal mortality and 80% of post-neonatal mortality,” the model estimates that a 16% reduction in post-neonatal diarrhea translates to a 13% reduction in all-cause mortality, while an 11% reduction in neonatal diarrhea translates to a 5% reduction in all-cause mortality. This modeling takes into account all non-diarrheal health outcomes that contribute to mortality, such as respiratory infections, but the mortality estimation uses diarrheal morbidity as the primary input.^[46] GiveWell’s CEA separately estimates “excluded effects,” or all effects other than all-cause mortality in infants aged <1 year,^[47] and applies an adjustment of 1.12x to overall program effectiveness.

The range of outcomes considered seems relatively comprehensive to us. However, we think age-specific effects could be considered more granularly—for example, modeling decreased benefits after the second month, or splitting the post-neonatal group into two or three subgroups. We also noticed that GiveWell does not explicitly consider potentially improved infant/child growth (or reduced stunting), although that is understandable given the relatively weak evidence for those effects. This might also overlap with all-cause mortality for children >1 year of age (one of the excluded effects) and/or development effects. If GiveWell values this outcome intrinsically, it may be worth adding another row to the excluded effects sheet.

In addition, GiveWell’s stated motivation for using diarrhea morbidity as the primary input for mortality modeling appears to be inconsistent with its actual mortality modeling. GiveWell (2023) states that anchoring on diarrhea morbidity is motivated by Tylleskär’s view that a “[r]eduction in enteric infections [is] the primary mechanism by which breastfeeding promotion lowers infant mortality” (footnote 24). However, the cost-effectiveness model indicates that GiveWell’s current modeling is motivated by “Assumption 4” in its mortality plausibility modeling for water quality interventions. Assumption 4 states that all GBD causes of death are affected proportionally to their overall share of all-cause deaths except the category “other neonatal disorders,” which is affected at 50% of the rate expected based on its share of all-cause mortality.^[48] Following naturally from this assumption,^[49] GiveWell’s mortality modeling finds that enteric infection-related deaths are not the top cause of deaths averted by breastfeeding promotion, for both post neonates and neonates (Figure 7). This inconsistency calls into question GiveWell’s use of the diarrhea morbidity reduction as the basis of its estimate of all-cause mortality reduction, as well as its actual view of the main mechanism by which breastfeeding promotion reduces infant mortality.

Figure 7: GiveWell’s current modeled reduction in mortality from breastfeeding promotion by cause

Note. Graph by Rethink Priorities based on GiveWell’s cost-effectiveness analysis.

We suggest three main options for addressing this inconsistency:^[50]

1. Keep the model as is. GiveWell could simply reframe the reduction in diarrheal morbidity as representing change in a general risk factor that is directly proportional to disease mortality for any given cause (e.g., reduced pathogen load for infections and general immune system benefits for other causes). This may be a good choice if there is not enough high-quality evidence on non-diarrheal morbidity, and has the additional benefit of being the simplest to implement.
2. Change Assumption 4. GiveWell could consider revising the assumption it uses to give greater weight to enteric diseases (perhaps somewhere between Assumption 1^[51] and Assumption 4). This may be a good choice if GiveWell gives some credence to both Tylleskär’s view that the reduction in enteric infection mortality is the “primary mechanism” for breastfeeding promotion lowering infant mortality and Assumption 4.
3. Change the morbidity reduction input. GiveWell could consider using a different morbidity reduction input (or set of inputs) that captures a broader range of the mortality causes under consideration, principally “respiratory infections and tuberculosis.” This may be a good choice if GiveWell gives significantly more credence to Assumption 4 than to Tylleskär’s view and can find high-quality evidence on non-diarrheal morbidity.

Health benefits by type of health outcome

When pressed for the share of breastfeeding’s health benefits associated with each type of illness, none of our first three experts were willing to venture a guess. One expert highlighted the potential for overlapping mechanisms, suggesting that interventions aimed at reducing one type of infection (e.g., diarrhea from waterborne pathogens) could also reduce susceptibility to other infections, like respiratory illnesses. This relationship, sometimes referred to as the Mills-Reincke phenomenon, suggests that improvements in environmental health factors (e.g., water quality or breastfeeding exclusivity) can lead to broader health benefits than initially hypothesized.

Prentice (2022), in a summary of meta-analyses, noted that “in low-income settings, the chief measurable benefits for the child are in respect of reductions in diarrhea and respiratory infections, and in mortality” (p. 29). The paper further claims that breastfeeding^[52] resulted in “estimated reductions of about a half for diarrhea and a third for respiratory infections” (p. 30). Our impression is that in low-income contexts with low water quality, diarrhea and waterborne illness likely account for a large portion of the health benefits of breastfeeding for children under six months, but we are unsure of the magnitude and of the share of benefits after the six-month mark. As discussed above in the section on health benefits by age, Tylleskär estimated that the benefits during earlier months are much more valuable than those in later ones; by his reckoning, breastfeeding in the second month is about 5x more important than in the 12th.

A note on the debate over water quality and infant illness

Our discussions with Lantagne and another expert highlighted an ongoing debate on the relationship between water quality, diarrhea, and mortality. At issue is whether the health risk from waterborne pathogen exposure has a linear dose-response relationship, or rather exhibits sharp threshold effects. Proponents of the “linear” model argue that reducing pathogen levels incrementally yields proportional health benefits, while proponents of a sharp threshold approach believe even low exposure can result in significant harm (akin to a “zero-tolerance” model).

Meta-analyses (e.g., Kremer et al., 2023 [working paper]; Clasen et al., 2007; Wolf et al., 2022) point towards significant mortality reductions among newborns due to water treatment, yet these benefits are not the studies’ primary outcomes, and thus are neither reported nor sufficiently powered. Some studies on water quality interventions such as the SHINE/WASH trials found mortality reductions but failed to find significant effects on stunting or other intermediate outcomes. These difficulties in identifying health benefits have led some grantmakers and researchers to question the mechanisms at play.

The disagreement extends to whether interventions like breastfeeding reduce mortality primarily through direct pathogen reduction (e.g., fewer cases of diarrhea) or via broader systemic effects (e.g., reduced secondary infections or malnutrition). A key challenge in the water quality debate is measurement: quantifying true exposure, identifying diarrhea as different from normal infant stool, and disentangling overlapping mortality risks from multiple causes, such as diarrhea, respiratory infections, and malnutrition. Such problems are especially serious when measuring breastfeeding, as issues of “uptake” and reporting bias may be considerably more severe, as discussed above.

We have found very little data on the relationship between breastfeeding intensity and health outcomes,^[53] limiting our ability to fully quantify the pathways through which breastfeeding benefits infant health at various intensities. We think that there is a dose-dependent relationship in health outcomes by breastfeeding intensity level, where EBF consistently outperforms partial breastfeeding, which in turn is better than no breastfeeding. However, we are uncertain about the shape of the dose-response curve at the predominant/exclusive boundary. Our guess is that it is highly context-dependent:

• In low-income settings with high prevalence of unclean water and/or other unsanitary complementary foods or liquids, there’s likely to be a sharp boundary effect.
• In higher-income settings with reliable, clean water and overall good sanitation, there’s likely to be a more muted boundary effect, and the health benefits of predominant breastfeeding and exclusive breastfeeding are likely much more similar.

We identified very few relevant studies directly comparing the effects of breastfeeding on mortality by intensity level in LMICs, and they do not lend support to a particular view. Sankar et al. (2015) conducted a meta-analysis that suggested a dose-dependent response of health benefits to increasing breastfeeding intensity. The study finds that all forms of breastfeeding—whether exclusive, predominant, or partial—are associated with reduced diarrhea and pneumonia incidence, improved survival rates, and long-term benefits like reduced obesity and higher cognitive outcomes. However, compared to EBF, predominant breastfeeding was associated with a 1.48 RR of all-cause mortality,^[54] partial breastfeeding with 2.84 RR, and no breastfeeding with 14.4 RR (Table 2, p. 8).

Figure 8: Effect of different breastfeeding intensities on all-cause mortality

Note. From Sankar et al. (2015), p. 9.

However, we would be wary of taking Sankar et al.’s (2015) results literally as they are not causal. As shown in Figure 8, the meta-analysis was performed on the basis of a very small number of observational studies. The “Predominant, partial or no BF vs. exclusive BF in 0-5 months of age comparison” involved the following studies (see Sankar et al., 2015, pp. 5-6, Table 1):

• Arifeen et al. (2001), a cohort study with n=1,677 in an urban slum in Bangladesh: Since this study was a prospective observational study, it does not indicate that breastfeeding promotion activities that cause a change in a mother’s breastfeeding intensity level would confer the same observed benefits.
• Bahl et al. (2005), an analysis of secondary data from an RCT with n=9,424 in urban/peri-urban settings in Ghana, India, and Peru: While the data are from an RCT, the trial did not involve any randomization of breastfeeding behaviors (which would likely be unethical), and the analysis was therefore based on an observational cohort design (with all the biases that entails).
• Edmond et al. (2006), an analysis of secondary data from an RCT with n=10,947 in rural Ghana: Similar to Bahl et al. (2005), while the data are from an RCT, the analysis is observational cohort-based and subject to bias.

Thus, even setting aside the issue of measurement bias, it appears that the meta-analysis has limited usefulness for thinking about the mortality dose-response relationship. An expert said that typical breastfeeding promotion trials are not powered to detect mortality differences well, while heterogeneity analyses that are sufficiently powered are unlikely to identify causal effects because there are likely systematic differences between groups with higher breastfeeding intensity. Furthermore, we do not think it is possible to characterize the shape of the dose-response relationship on the basis of these categorical data (partial breastfeeding spans an extremely broad range of possible intensities).

Some studies also indicate that EBF is associated with lower morbidity than partial and predominant breastfeeding. Agrasada et al. (2011) observed in an RCT in Manila that partially breastfed infants had greater morbidity than their exclusively breastfed counterparts, particularly from gastrointestinal and respiratory infections (p. 64). In rural Sierra Leone, Koroma et al. (2024, observational study) observed that infants exclusively breastfed at six weeks had a lower mortality risk compared to non-EBF infants (p. 6). Penugonda et al. (2022), in an observational study in India, found fewer illnesses and lower mortality among EBF infants compared to partially or non-breastfed infants (p. 1482). The randomized studies discussed in question 1 (e.g., Kramer et al., 2001) do not break down morbidity or mortality outcomes by breastfeeding intensity levels, though, even if they did, that would likely not help clarify the true dose-response relationship.^[55]

Evidence on the relationship between breastfeeding and waterborne illness

Partial breastfeeding offers some limited protection from waterborne illness. Agrasada et al. (2005, RCT in Manila, Philippines) showed that low-birthweight infants exclusively breastfed for six months had zero incidence of diarrhea, whereas partially breastfed infants experienced higher rates, although still lower than non-breastfeeding (abstract). Agrasada et al. (2011, RCT in Manila) reinforced this dose-response relationship, showing that exclusively breastfed low birth weight infants had zero days of diarrhea over six months, compared to 2.3 days for partially breastfed infants and 2.5 days for non-breastfed infants (p. 64). Khin et al. (1985, RCT in Rangoon, Burma) demonstrated that “continued breastfeeding” during acute diarrhea significantly reduced the number and volume of stools, shortened illness duration, and reduced the need for ORS compared to non-breastfed infants (p. 588). North et al. (2022), in a review, noted reductions in diarrhea morbidity and mortality even in partially breastfed infants but emphasized that EBF offers the highest level of protection (p. 230).

Evidence indicates that general “breastfeeding promotion” protects against diarrhea, even when breastfeeding behavior likely does not shift entirely to EBF. In Kibera slum, Kenya, Ochola et al. (2008, randomized controlled trial) found that intensive, home-based breastfeeding counseling increased EBF rates to 23.6% at six months compared to 5.6% in controls. Infants in the intervention group then experienced significantly lower rates of diarrhea and underweight outcomes. The study did not report results for intensities of breastfeeding other than exclusive and “non-exclusive.” Dib et al. (2023) highlighted in a meta-analysis of RCTs that EBF interventions had a borderline significant effect on diarrhea reduction (OR = 0.84; 95% CI: 0.70–1.00), with variability in outcomes likely due to population differences (p. 57). Lassi et al. (2020), in a literature review, reported a 24% reduction in diarrheal diseases through breastfeeding promotion efforts (p. 10).

Observational studies generally find that EBF is associated with lower gastrointestinal illness compared to lower intensities of breastfeeding. Kamal et al. (2024), in a cross-sectional study in low-income settings, observed a 40% lower incidence of diarrhea among exclusively breastfed children compared to those who were partially breastfed or formula-fed (abstract). Frank et al. (2019), in a cohort study, reported a 45% reduction in gastroenteritis odds among EBF infants (p. 6, Table 2). Ogbo et al. (2017), in a survey study of Sub-Saharan African data, found that introduction of complementary foods (OR = 1.31; 95%CI: 1.14–1.50) was significantly associated with a higher risk of diarrhea (p. 8). Hoyle et al. (1980), in an observational study, found that breastfeeding helped mitigate reductions in food intake during acute diarrheal illness, compared to non-breastfeeding (abstract).

Horta (2019) synthesized multiple reviews, finding that EBF is associated with 80% lower diarrhea morbidity (RR = 0.20) and 77% lower mortality (RR = 0.23) in infants under six months, compared to those who were not breastfed at all (p. 1). Hamer et al. (2022) found in a review that regional reductions in diarrhea prevalence were associated with EBF (as compared to later initiation and non-exclusive intensities) across South East Asia, Western Pacific, Eastern Mediterranean, and African regions (p. 1).

Respiratory illness

Studies also show that respiratory infections are significantly reduced by breastfeeding across intensities, with EBF demonstrating the most substantial effects. Dib et al. (2023) found a 59% reduction in respiratory illness odds among infants aged 0–3 months whose mothers had received EBF interventions (OR = 0.41), though the effect did not persist (p. 57, meta-analysis of RCTs). Kamal et al. (2024) similarly reported 39.7% lower pneumonia incidence and 32% lower incidence of colds among exclusively breastfed children (abstract). Frank et al. (2019) documented a 24% reduction in otitis media among EBF infants (p. 6, Table 2).

However, non-exclusive breastfeeding does also appear to be associated with respiratory infection, and general interventions to promote breastfeeding appear to reduce health issues arising from respiratory illness. For example, Horta (2019) reported in a review that “breastfeeding” is associated with a reduction in respiratory infection morbidity by 32% (RR = 0.68) and mortality by 70% (RR = 0.30) in infants and young children (p. 1). Ariff et al. (2020) observed modest reductions in both upper respiratory tract infections (4%) and lower respiratory tract infections (3%) following breastfeeding promotion interventions (p. 6).

Respiratory illness, like diarrhea, is often measured using subjective symptoms such as cough or fever. In our interviews, Lantagne and one additional expert emphasized the challenges of relying on parent-reported data for symptoms, which can be prone to bias, particularly in observational studies. Such measurement issues particularly arise for diarrhea and respiratory illnesses, which often don’t have clear definitions and are defined more by symptoms than by other types of medical analysis. One expert said, however, that maternal reports of infant diarrhea are likely less susceptible to social desirability bias than those of breastfeeding intensity.

The Kramer et al. (2001, RCT in Belarus) results further complicate this picture, as the intervention significantly increased EBF rates and reduced gastrointestinal infections but showed no significant reduction in respiratory infections between intervention and control groups.

Non-communicable diseases, growth, and long-term outcomes

Breastfeeding at various intensities is associated with reduced risks of non-communicable diseases. Ariff et al. (2020) noted a 5% reduction in skin lesions among infants who received a breastfeeding support intervention, indicating likely ancillary health benefits even when breastfeeding is not exclusive (p. 6, cohort study). Thomaz et al. (2018) found in a meta-analysis that breastfeeding, whether mixed or exclusive, was associated with protection against dental issues such as open bite and crossbite, with stronger effects for longer breastfeeding durations (abstract). Kim et al. (2021) found that EBF for 4–6 months reduced hospitalization rates and risks of neurological, respiratory, and gastrointestinal conditions (p. 9).

For long-term outcomes, Prentice (2022) highlighted that “breastfeeding” (not just EBF) is associated with improved IQ scores of 2–3 percentage points, offering cognitive and developmental advantages that can persist into adulthood (p. 29). These findings align with Horta (2019), who reported associations between “ever breastfeeding” and greater educational attainment and lifetime income (p. 1). Kamal et al. (2024) further associated EBF with superior cognitive performance, with 34.2% of exclusively breastfed children rated above average compared to 6.5% in the formula-fed group (abstract).

For the most part, studies have demonstrated that exclusivity is correlated with reduced stunting in LMICs, although all evidence we have found is observational. Hadi et al. (2021) found that exclusively breastfed children under two years old from poorer households were 20% less likely to be stunted than their non-EBF peers (p. 7). Similarly, Koroma et al. (2024), in rural Sierra Leone, observed superior weight and length gains among EBF infants at six weeks (p. 6). Haque et al. (2023) also identified EBF as a key factor in reducing stunting prevalence, with benefits observed across intervention and control groups in the Suchana program (p. 8). Experts also pointed to the capacity for continued breastfeeding to fill urgent caloric gaps in emergency and famine contexts. Tylleskär pointed out that this could be a key route in which continued breastfeeding could reduce malnutrition and stunting in children older than six months, and Lantagne referenced the fragile supply chains for formula and other calorie sources.

However, Lassi et al. (2020), in a systematic review of breastfeeding education interventions in LMICs, showed that supplementation seems to have better effects than EBF at improving infants’ physical growth (p. 8). Agrasada et al. (2011, observational study in Asia) reported no significant differences in weight, length, or head circumference between exclusive, partial, and non-breastfed infants over six months (p. 66).

Long-term benefits also commonly highlight breastfeeding’s protection against obesity, although all evidence we have found is observational. Ardic et al. (2019) found that EBF for at least six months significantly lowered the risk of childhood obesity (p. 32). Mantzorou et al. (2022), similarly found that EBF was associated with lower overweight and obesity prevalence among both Greek mothers and children up to five years post-delivery (p. 9). Tambalis et al. (2018), again in Greece, reported a 30% lower risk of childhood obesity (OR = 0.70) and a 38% lower risk of adolescent obesity (OR = 0.62) with EBF for six months or more (abstract). Although this particular health concern may be less of interest in GiveWell-relevant contexts, we believe it is worth including in this review as it may indicate long-term markers of health that are less well-understood.

Contributions and acknowledgments

Ruby Emerson and James Hu jointly researched and wrote this report as project co-leads. Jamie Elsey conducted additional modeling, authored Appendix D, and assisted with data visualization. Greer Gosnell supervised the project.

Special thanks to Meika Ball and Aisling Leow for helpful comments on drafts. Thanks also to Shane Coburn for copyediting and Sarina Wong for assistance with publishing the report online. Further thanks to Michael Kramer, Daniele Lantagne, and Thorkild Tylleskär for taking the time to speak with us.

GiveWell provided funding for this report, but it does not necessarily endorse our conclusions.

Appendices

Appendix A: Effects of breastfeeding promotion programs on exclusive breastfeeding rates in LMICs

As a starting point, we found consistent (though likely very biased) evidence that breastfeeding promotion programs are effective at increasing exclusive breastfeeding rates in LMICs. For example, GiveWell’s (2023) CEA for breastfeeding promotion (see here and here^[56]) indicates that every RCT included in GiveWell’s meta-analysis of breastfeeding promotion on diarrhea morbidity (see here) and every experimental/observational study included in Olufunlayo et al.’s (2019) systematic review and meta-analysis (see here and Figure A1) showed an increase in exclusive breastfeeding rate due to or after a breastfeeding promotion program. Our review of the literature largely affirmed this finding: several systematic reviews (Olufunlayo et al., 2019; Tadesse et al., 2018; Chipojola et al., 2020; Lassi et al., 2020) highlight breastfeeding promotion programs’ consistent success in increasing exclusive breastfeeding rates and other outcomes like early initiation.

At the same time, these studies exhibit considerable variability in intervention effect size on exclusive breastfeeding rate. For example, in the 10 trials used by GiveWell in its meta-analysis of breastfeeding promotion on diarrhea morbidity, the average increase in exclusive breastfeeding rate was 383%, with a range of 18% to 1217% (here), while Olufunlayo et al. (2019)’s estimated effect size of 2.19 (re-estimated by GiveWell to be 2.26^[57]) has a 95% confidence interval of 1.73 to 2.77 and a prediction interval of 0.81 to 5.94.

Figure A1

Note. From Olufunyalo et al. (2019), p. 13.

Appendix B: Recent paper on the extent of bias in maternal reports of breastfeeding outcomes

Stewart et al. (2024) investigated the extent of three potentially biased outcomes in a randomized controlled trial conducted in Kenya and found “strong evidence of bias in reporting of breastfeeding practices” (abstract). The trial involved administering a behavioral program promoting exclusive breastfeeding to a subset of mothers^[58] and collecting self-reported breastfeeding outcome data up to five times at different follow-up periods (up to two years).

• They found especially strong evidence that maternal reports of EIBF were biased. The trial initiated health promotion activities only after 40% of mothers had given birth to their infants. The authors identified mothers whose infants were born pre-initiation, and who therefore could not have altered their “true breastfeeding initiation behavior” in response to the program. They found that, among these mothers, there was a 25.6 percentage point increase in self-reported EIBF in the treatment group over the control group (as compared to a 26.5 percentage point increase found in mothers whose infants were born post-initiation). Thus, they concluded that “the intervention effect can be nearly entirely attributed to recall bias” (p. 6).

Figure B1: Prevalence of early initiation of breastfeeding stratified on timing of birth

Note. From Stewart et al. (2024), p. 5.

• They also found compelling evidence that maternal reports of EBF duration (age of EBF cessation) were biased. The authors analyzed the degree of inconsistency in reporting of age of EBF cessation in the treatment and control groups and found that, between six and nine months post-birth, mothers in the treatment group were significantly more likely than those in the control group (75.9% compared to 32.5%) to revise an initial report of <6 months EBF duration to ≥6 months. During the period from six to nine months post-birth, treatment-group mothers were exposed to more intervention messages while control-group mothers were not, which could have increased the treatment group’s susceptibility to social desirability bias. That said, the overall within-person error did not differ significantly between the two groups.

Figure B2: Response consistency over survey rounds among women with multiple EBF duration reports

Note. From Stewart et al. (2024), p. 6.

Appendix C: Detailed qualitative insights from expert interviews

Theme 1: Empirical and data limitations

• All experts said that they were not familiar with specific data or analyses about breastfeeding intensity distribution changes. Michael Kramer said that if any such analyses have been done, the Family Larsson-Rosenquist Foundation (the only philanthropic foundation that is specifically devoted to funding and implementing breastfeeding research) would likely be aware. (He also expressed skepticism about the importance of our research question, saying that while it is of theoretical interest, he would prefer to see more work on child growth, health, and long-term effects.) While we did not hear back from the foundation after reaching out to its director, Katharina Lichtner, we think it’s very likely that such work has not been done before and the relevant data do not exist (beyond what are included in this report).
• An expert interviewee who was an author on Stewart et al. (2024) explained various aspects of breastfeeding behavior measurement challenges in our interview.
  • In addition to being susceptible to bias, the expert said that breastfeeding behavior surveying generally produces a “cross-sectional snapshot of an individual at a given point in time” and thus can fail to capture the dynamic practice of breastfeeding over time. Thus, an answer of “exclusive” over a recall period of 24 hours does not necessarily imply exclusive breastfeeding since birth. A number of relatively recent trials have used multiple recall periods (within-subject), which show that mothers report lower EBF rates over longer recall periods (e.g., Tylleskär et al., 2011, p. 423; Yotobieng et al., 2015, p. e549).
• Some experts also pointed to study design limitations in breastfeeding promotion trials:
  • Kramer said that “most of the breastfeeding promotion programs, including PROBIT, start with women who intend to breastfeed. … There are no data, or virtually no data, on taking a mother who intends to formula-feed and somehow intervening around the time of birth.” We could not confirm whether such selection bias existed in our review of studies, which mostly do not mention whether mothers had an intention to breastfeed, and are additionally uncertain about the directional effect on the effectiveness of promotion on non-breastfeeders implied by this potential bias. If women with no intention to breastfeed have no intention because they lack something provided by the intervention, one might expect greater intervention effects. If they have no intention because they have characteristics that correlate with low persuadability through intervention, one might expect lower intervention effects.
  • One expert pointed to inconsistencies in recall period that make it difficult to compare results across trials. They said, “Even with the randomized controlled trials, different research groups used different periods of recall, and they’re all, for the most part, [cross-sectional] snapshots. They’re not prospectively collected day to day over a six month period of time.” Our review of studies was consistent with this comment: Kramer et al. (2001) used recall over the whole postnatal period for the first follow-up and recall since the last follow-up for subsequent follow-ups (elicited monthly, then quarterly), while Bhandari et al. (2003) used recall over the past 24 hours (elicited only once).

Theme 2: Breastfeeding intensity transitions over time

• Experts said that breastfeeding intensity in a given mother-infant dyad tends to decrease with time and that reversals are rarely seen:
  • Kramer: “If a woman is already partially breastfeeding, if that has been the result of coming down from more exclusive breastfeeding to 50% partial, it’s unlikely to go back the other way. Because there’s usually a reason, either the mother didn’t feel like or really couldn’t produce enough breast milk to satisfy the baby, or more frequently in many countries, particularly in Asian countries, where women go back to work at four to six months.”
  • Another expert: “Once an individual has decided to introduce other liquids or solids, it’s, I think, a harder behavior to go back to exclusivity, and it’s an easier behavior to continue that practice or introducing more and more other things.”
• Kramer said that partial breastfeeding is “almost always a transition period. … The mother’s milk supply dries up quickly.” However, he said, some women can maintain a 50% partial regimen [of feedings as breast milk] and that some women, typically those “who have been breastfeeding for a long time,” can even sustain a “one or two breastfeedings a day.”
• Tylleskär sees the start of breastfeeding (early initiation of breastfeeding) as the most critical point at which to intervene, and said that doing so essentially induces a trajectory change: “If you get a bad start, you’re likely to end early. The ones that get a good start are likely to breastfeed and have a good time with the baby.”
• During our interview, Tylleskär shared a graph showing the ideal pattern of infant and child feeding, where complementary foods are introduced at six months (at which point breast milk stops being nutritionally sufficient for the infant) and family foods are introduced around nine months.

Figure C1: Ideal pattern of infant and child feeding

Note. Screenshot of figure shared by Thorkild Tylleskär during Zoom interview.^[59]

Theme 3: Impact pathways and barriers to breastfeeding

• One expert broke down the process of behavior change through breastfeeding promotion programs as follows: “The intervention is providing information to caregivers [including mothers]. … So you hear information, and then you have a change in knowledge about the thing. Then you change your intention, and then you change your behavior.” They noted that there is “strong evidence of an improvement in knowledge” but the field lacks “hard data on the change in [breastfeeding] practice.”
  • When prompted about the existence of diarrhea morbidity outcome data^[60] that might, in a trial context, indicate a health benefit from an actual change in breastfeeding practice, they agreed that this would “give more credence to the fact that behavior would have changed,” though she noted not all studies measure growth and diarrhea.
• Multiple experts noted that the mother often does not have full autonomy in her decision to breastfeed and that her mother, mother-in-law, and other relatives are likely to influence her decision. Experts emphasized that community acceptance and support of breastfeeding can also influence the individual mothers’ (ability to make their own) breastfeeding decisions:
  • Kramer: “When the feeding [formula or breastfeeding] decision is made, it’s not just the mother’s decision, it’s the grandmother’s decision, it’s the sister’s decision, it’s the husband’s decision, it’s the pediatrician’s decision.”
  • Tylleskär: “The young mother is not running the show. All of a sudden, there is the mother-in-law. There is the mother of the mother. There is a whole group of people that are now taking over the baby and telling her what to do, etc. And the pressure is very big. And the young mother is not able, on her own, to resist to all this, so she gives up and lets them do whatever should be done.”
  • Another expert: “There’s social acceptability and support for any breastfeeding, and then there’s a second layer to that, which is acceptance and support for exclusive breastfeeding. And so in it, in a given culture, there may be high acceptance for breastfeeding, but not for exclusivity in children under six months of age. And so the way that may be visible is in kind of social commentary that may come from mothers or grandmothers … who may say things like, ‘Oh, you know, you should be giving more. You should be giving more food.’”
• Tylleskär strongly emphasized the threat posed by the commercial milk formula industry, and said that “the biggest threat to breastfeeding is the commercial entities” that deploy irresponsible and deceptive marketing tactics. Tylleskär stressed that breastfeeding promotion programs must address competition from commercial marketing. As an example, he said that marketers wearing white coats go directly to hospitals to distribute formula samples to new and expecting mothers. He added in a later email that there are “enormous efforts in social media [which make use of influencers] to sow doubt in young mothers’ minds about their ability to breastfeed.”
  • In The Lancet’s 2023 series on breastfeeding that Tylleskär suggested we read, the leading editorial lambasts the industry for “underhanded marketing strategies, designed to prey on parents’ fears and concerns at a vulnerable time” and calls for greater government regulation of misinformation about breastfeeding and of ensuring manufacturers are held to the International Code of Marketing of Breast-milk Substitutes (The Lancet, 2023, p. 409).

• Multiple experts said that a lack of workplace support for breastfeeding can inhibit breastfeeding uptake for some women, although one noted that such policies have little relevance for subsistence farmers. Conversely, one other expert said that rural women who work in subsistence agriculture have higher rates of breastfeeding because they can easily bring their babies to their workplaces. The pressure to return to work can also cut short the period of high-intensity breastfeeding.
  • One expert: “We don’t have good workplace supports for women who even have good intentions and good knowledge … But for farmers, whatever the government policy is, doesn’t matter. You still have crops in the field. You have work that needs to be done, and someone has to do it.”
  • Lantagne: “There’s a decent amount of data that, at least in low-income countries, that rural women have much higher rates of breastfeeding and of exclusive breastfeeding … because their work, which may be fields or whatever, the baby’s with them.”
  • Kramer: “Particularly in Asian countries, where the women go back to work at four to six months… that’s all they can manage.”
• Lantagne also noted the potential risks of HIV+ mothers breastfeeding their children,^[61] and further potential stigma against non-exclusive breastfeeding as a possible barrier to programs’ capacity to increase breastfeeding intensity.

Theme 4: Disadvantages of breast milk alternatives and complements

• Lantagne described several risks to using formula. First, formula supply chains are often fragile in low- and middle-income countries, and mothers who have already started to formula-feed their infants but cannot reliably access the product may be forced to introduce alternative foods earlier than ideal. Second, bottled milk develops bacterial growth easily and it is not safe to continue feeding a child an unfinished bottle of formula due to this growth, although “education is needed for caregivers on the risks of infants consuming leftover bottle milk.”
• In addition to potentially exposing infants to pathogens in unsanitary water, breast milk alternatives and complements are described by experts as nutritionally less dense than breast milk.
  • Tylleskär described complementary feeding as involving “different types of gruel” that are nutritionally less dense than breast milk; he said that children who eat these foods need to eat greater volumes to compensate for lower caloric density, but in practice they tend to simply eat fewer calories than they need.
  • Another expert similarly described complementary foods and liquids that are typically offered in Kenya as “very thin porridges” with “very poor” nutritional content and caloric density.

Appendix D: Modeling of intervention effects on breastfeeding intensity

One possibility we have raised in this report is that the breastfeeding interventions reported by Kramer et al. (2001) and Bhandari et al. (2003) may have had similar effects, but that the baseline/control group levels of breastfeeding in each study could belie this similarity. We also considered whether the intervention might impact different breastfeeding levels to a greater or lesser extent. To fully assess these possibilities, we would want access to all the individual-level outcome data, as well as possible variables/confounds to control for, which was unavailable to us. This could include information about the administration of the treatment over different locations and corresponding location-level predictors, which could also affect the estimates.

However, it is possible to get an intimation of whether the effect sizes of these two studies might be similar on the basis of the summary information. We can do this using a cumulative ordinal model of the breastfeeding intensity outcomes (Bürkner & Vuorre, 2019). Such a model seeks to explain the ordinal outcomes as reflecting a latent normal distribution that underpins the observed outcomes, with cutpoints along the distribution that separate people into the respective ordinal categories (None, Partial, Predominant, and Exclusive).

In this type of model, an intervention can be seen as shifting the latent normal distribution up or down, such that the likelihood of falling into the different ordinal categories is correspondingly changed. The extent of this shift is then essentially an effect size, represented in standard deviation units, attributable to the intervention. The latent distribution to some extent can be thought of as something substantive that underpins or leads to people being categorized a certain way (e.g., motivation and self-efficacy for breastfeeding that is increased or decreased, causing people to then engage in behaviors that result in their ordinal categorizations), although ultimately it is something of an unobserved statistical abstraction/tool used to explain how the observed ordinal outcomes could be produced.

Using the numbers of people who were included in each of the studies and conditions at three months, and the percentages of them that fall into each breastfeeding category, we can construct such a model and assess whether the effect sizes of each intervention are similar to one another. We would stress again, however, that this is imperfect. Ideally, we would have access to individual data and be able to control for possible confounding individual-level characteristics that might end up changing the effect size estimates. The uncertainty intervals associated with the outcomes are likely to be overly precise. In addition, if there is very little commonality in what the different levels of the breastfeeding scale represent in the different studies, despite their similar labels, this would also challenge the validity of combining the two sets of outcomes in the same analysis^[62].

Simplest model

The simplest model we ran was a cumulative ordinal model with a probit^[63] link, with a study (Bhandari vs. Kramer) by condition (control vs. treatment) interaction. Parameter estimates from the model supported the ideas that: 1) the treatment effect was reliably positive (see the treatment parameter), 2) the treatment effect varied relatively little across the two studies (see the treatment x Kramer parameter, which is the change in the treatment effect for the Kramer study relative to the Bhandari study), and 3) the respondents in the Kramer study started at a lower baseline level (the Kramer parameter).

Figure D1: Parameter estimates in simplest model

When plotting the expected values from this model, however, there was a potentially unacceptably large mismatch between the modeled outcomes and the observed outcomes that the model was intended to capture/represent.

Figure D2: Mismatch between modeled and observed outcomes in the simplest model

Model with category-specific effects

A further extension of the model can add “category-specific” effects, whereby the cutpoints themselves may also shift with the intervention. This can expand or contract the width of certain ordinal bins on the latent scale, such that when an intervention is administered, people may more or less easily “pass through” or “fall into” certain ordinal values. However, it should be noted that doing so can also add difficulty in interpreting the relative intervention effects, as the treatment effect now operates through more than one process (shifting the latent scale, and changing the cutpoints), as opposed to readily interpretable main effects and interactions.

Such a model did seem to better (though still imperfectly) capture the patterns in the observed data.

Figure D3: Mismatch between modeled and observed outcomes in model with category-specific effects

Parameter estimates for the model again suggested that, in general, participants in the Kramer study began with a lower baseline (the Kramer parameter), but that the treatment in Bhandari (the Treatment parameter) did not reliably produce a general shift upwards in the latent scale. The positive Treatment x Kramer parameter indicates that for the participants in Kramer, there did tend to be a general shift upwards in the latent scale. However, the category-specific effects suggest another way in which the treatment was operating: the shift in cutpoint 3 is reliably and substantially negative, while that of cutpoint 2 is almost exactly zero. This would have the effect of compressing the latent space attributed to “Predominant” breastfeeding and expanding that of the “Exclusive” category, such that people are more likely to fall into the topmost category (“Exclusive”), and more readily pass through the “Predominant” category.

Figure D4: Parameter estimates in model with category-specific effects

Whereas with just a shift in the latent scale, it was quite natural to interpret the effects as being a shift in some substantive underlying latent variable (such as breastfeeding motivation and self-efficacy), it can be more difficult to provide a substantive interpretation as the model becomes more complex with category-specific effects. It might be suggested, for example, that one way in which the treatment is operating is by specifically facilitating a shift from the predominant to the exclusive category (perhaps by reducing some kind of barrier), such that large increases in some underlying capacity are not necessary to drive changes in observed behavior. However, this is highly speculative, and these underlying capacities are not measured. It may be better to simply treat the parameters as more of an abstract and statistical explanation: the outcomes in the two studies can be reasonably well explained/modeled as being the result of a general shift upwards, starting from a lower baseline, for Kramer participants, as well as a more specific contraction in the likelihood of breastfeeding “predominantly” in both studies. Both studies thus had a positive impact on the outcome of interest, but may have done so through partially different means.

The plot below depicts how the average parameter estimates from the model explain the observed data.

Figure D5: Estimated latent distribution and ordinal cutpoints

Note. Vertical black lines are cutpoints, numbered 1, 2, and 3 from left to right.

Appendix E: Evidence from US-based studies

We briefly looked into the effects of breastfeeding promotion programs in high-income countries, but came away with the impression that the evidence was unlikely to be meaningfully higher-quality than that in low- and middle-income countries. Therefore, we decided to deprioritize this section, which was originally written up as a subsection of Q1a.

In addition to papers from low- and middle-income countries, we identified three papers (Bonuck et al., 2014; Bonuck et al., 2005; Ahmed et al., 2016) that have similar outcome variables (exclusive, predominant, partial, none) but in the US context.

Bonuck et al. (2014) evaluated two studies: Provider Approaches to Improved Rates of Infant Nutrition & Growth Study (PAIRINGS) which compared usual care to a combination of pre- and postnatal visits with a lactation consultant (LC) and electronically prompted guidance from prenatal care providers (EP), and the Best Infant Nutrition for Good Outcomes (BINGO) study, which had 4 arms: usual care, LC alone, EP alone, or LC+EP. The study measured breastfeeding intensity (categorically as “low”, “medium”, “high,” but constructed from quantitative data) representing the percentage of feedings that are breast milk.

Since the data collected in Bonuck et al. (2014) are not public, we requested the data from Karen Boncuk over email. Bonuck said that she cannot locate the data, and that none of her coauthors have a copy. Our intention for requesting the data was to better understand intervention effects by intensity over time, with the potential to adjust the attrition dynamics for different baselines and contexts, despite the data’s limited applicability for any context in which GiveWell is likely to operate.

The PAIRINGS intervention showed across-the-board (i.e., both “medium” and “high”) increases in intensity at six months postpartum. However, at one and three months postpartum, the effect seems concentrated in promoting exclusive breastfeeding. Similarly to PAIRINGS, the BINGO intervention seems to show across-the-board increases in intensity at six months postpartum, but effects seem concentrated on exclusive breastfeeding at one and three months.

Figure E1: Bonuck et al. (2014) Table 2

Bonuck et al. (2005) found across-the-board effects with a large decrease in non-breastfeeding in the intervention group, but notably only a very small effect on the exclusive breastfeeding rate. However, the intervention did not seek to promote exclusive breastfeeding; it supported women in breastfeeding by providing lactation consultants.

Ahmed et al. (2016) also seem to show across-the-board increases in all (both) breastfeeding intensity groups other than exclusive formula due to intervention at two and three months postpartum, though the effect is concentrated among exclusive breastfeeding at discharge and at one month postpartum.

Figure E2: Ahmed et al. (2016) Table 4

1. It is possible to measure and classify breastfeeding practice over a two-week period with an objective stable isotope measure, using a method known as the deuterium oxide dose-to-mother technique. The technique involves comparing saliva samples of the mother and infant (see, e.g., Lopez-Teros et al., 2017, pp. 3-4 for a description of the technique). In our interview, one of the authors suggested that it would be expensive and impractical to scale the technique in large-scale breastfeeding promotion trials and that past studies that have used the technique have had small sample sizes and were generally not conducted in trial contexts. ↑
2. “Several studies have reported substantial differences between maternal reports of EBF when compared with that determined by the isotope method [15–19]. For example, a study of 1–5-mo-old infants in Cameroon using dietary recalls since birth found substantial overestimation of reported EBF (45%) compared with that determined by the isotope method (11%) [18]. Similarly, a study of Indian infants found discrepancies between maternal reports of EBF over the past 24 h to that as determined by stable isotopes at 1 mo (100% reported EBF compared with 56% by the isotope method), 3 mo (90% reported EBF compared with 23% EBF by the isotope method), and 6 mo (36% reported EBF compared with 14% by the isotope method) of age [16]. Conversely, a study in Bangladesh found that there was a similar estimated prevalence of EBF at 3 mo between maternal recall over the past month (78%) and the deuterium method (82%), although there was also evidence of misclassification in reporting of both exclusive and non-EBF groups [19]. It is worth noting that the periods of assessment for these validation studies often do not match (i.e. a 14-d period for the isotope method compared with a 1-d, 1-m, or since birth maternal recall). One study in Ethiopia found substantially different estimates of the prevalence of EBF using a single 24-h recall (71.4%) compared with 14 cumulative 24-h recalls (47.1%) [36], which may reflect true day-to-day variation in feeding practice” (Stewart et al., 2024, p. 7). ↑
3. For example, programs appear more effective at causing otherwise predominantly breastfeeding women to switch to exclusive breastfeeding than at causing otherwise non-breastfeeding women to switch into higher categories. ↑
4. Here we are referring to the average breastfeeding intensity of breastfeeding in a population absent intervention, not to the prevalence of a particular intensity category. ↑
5. In other words, the “across-the-board”-ness of program impact is unlikely to depend heavily on baseline breastfeeding rates in the targeted population. ↑
6. The Bhandari study population had much higher baseline breastfeeding rates (2.9% non-breastfeeding in the control group at three months postpartum) than the Kramer study population (40.0% non-breastfeeding at three months postpartum). ↑
7. That said, we do not think there exist data on the effect of breastfeeding promotion on a continuous breastfeeding intensity outcome (e.g., percentage of feedings from breast milk) in LMICs. ↑
8. Our current understanding is that GiveWell’s evidence for breastfeeding promotion’s (BP) effects on mortality primarily comes from 10 studies (in six papers), which describe BP’s effects on diarrhea morbidity, prompting us to begin our review with these six papers. We then moved on to other RCTs identified by GiveWell in its 2018 review of breastfeeding that were not included in the meta-analysis (because they did not report diarrhea outcomes). Finally, we looked into the studies included in the Olufunlayo et al. (2019) meta-analysis. ↑
9. e.g., a mother choosing to exclusively breastfeed for an extra month instead of going down to predominant breastfeeding would be counted as a “predominant-to-exclusive flow.” ↑
10. i.e., a “predominant-to-exclusive flow” does not mean a mother has gone from predominant back up to exclusive breastfeeding. According to experts, reversals in intensity reduction are rare (see Appendix C). ↑
11. “Classification into breastfeeding categories reported at the 3-month visit was based on 24 h dietary recall, and the proportion of children fed exclusively on breastmilk during the first 4, 5, and 6 months of life was based on data obtained at the 9-month visit” (p. 1419). ↑
12. “Trained nutritionists did 24 h dietary recalls at the 3-month visit” (p. 1419). ↑
13. This assumption ignores the possibility that the program could have backfired in some cases. While we believe this assumption is reasonable, such negative program effects may be possible. In our interview, Daniele Lantagne noted that programs focusing only on exclusive breastfeeding may simply “make people feel guilty,” and that it might be a better approach to “help people move up a rung in the ladder.” ↑
14. Here we determined the maximum, not by assuming maximal inflow from lower intensities, but by taking the size of the control group directly. This is because naively assuming maximal inflow from lower intensities would mean a gross outflow of 31.1 percentage points from predominant, exceeding the actual size of the predominant category (at control). It is also for this reason that some of the inflow to exclusive must come from partial or none. ↑
15. We know that at least 3.9 percentage points of the gross/net inflow to exclusive must come from partial, because partial can contribute at most 6.4 percentage points of the gross inflow to predominant. ↑
16. This requires all non-breastfeeding mothers to switch to partial breastfeeding, and thus none of them to exclusive breastfeeding. Thus, the maximum proportion of the inflow to exclusive from partial and none remains 33%, and is not 37%. ↑
17. However, two of the original 34 hospitals refused to participate after randomization, and data from one polyclinic was excluded after it “was discovered to have falsified their outcome data” (p. 415). ↑
18. Study sites “were originally paired according to geographic region within Belarus (Minsk city, Minsk region, Brest, Mogilev, Gomel, Vitebsk, and Grodno), urban vs rural status …” (p. 414). Ultimately, the study “used a dichotomous stratification for region, west (Brest and Grodno) vs east (all others), and urban vs rural location” (p. 416). ↑
19. This is in line with the paper’s description of the time points at which polyclinic pediatricians were to complete a data form containing information about infant feeding: “At 1, 2, 3, 6, 9, and 12 months, polyclinic pediatricians completed a data form containing detailed information about infant feeding; measurement of infant weight, length, and head circumference; the occurrence of symptoms of gastrointestinal or respiratory tract infection, rash, other illnesses; and hospitalizations since birth or the most recent clinic visit” (p. 415). ↑
20. As Table 2 of the paper shows, there was not significant over- or underreporting of breastfeeding at three months postpartum in polyclinic chart versus maternal interview (p. 417). ↑
21. Thus, we think predominant actually means “predominant or exclusive,” and partial means “partial or predominant or exclusive.” ↑
22. By contrast, 67%-87% of the inflow to exclusive was from predominant in Bhandari et al. (2003); see here. ↑
23. Just from eyeballing; we did not calculate a quantitative measure of this. ↑
24. Here we determined the maximum, not by assuming maximal inflow from lower intensities, but by taking the size of the control group directly. This is because naively assuming maximal inflow from lower intensities would mean a gross outflow of 23.6 percentage points from predominant, exceeding the actual size of the predominant category (at control). It is also for this reason that some of the inflow to exclusive must come from partial or none. ↑
25. We know that at least 2.3 percentage points of the gross/net inflow to exclusive must come from partial, because partial can contribute at most 8.6 percentage points of the gross inflow to predominant. Subtracting this amount (8.6 percentage points) from 10.9 percentage points (the lower bound outflow from partial), we obtain 2.3 percentage points. ↑
26. This requires all non-breastfeeding mothers to switch to partial breastfeeding, and none of them to exclusive breastfeeding. Thus, the maximum proportion of the inflow to exclusive from partial and none remains 33%, and is not 37%. ↑
27. Either partial or none could account for the entirety of the inflow. ↑
28. “All women in the present study group were followed-up with regard to exclusive breastfeeding by telephone interviews at 7 and 14 days, 1, 2, 3, 4, 5, and 6 months after delivery and by home visits in cases that had problems with exclusive breastfeeding” (p. 1011). ↑
29. “Classification into breastfeeding categories reported at the 3-month visit was based on 24 h dietary recall” (p. 1419). ↑
30. “Secondary outcomes included … the prevalence of any breastfeeding at 3, 6, 9, and 12 months of age; and the prevalence of exclusive and predominant breastfeeding at 3 and 6 months” (p. 415). ↑
31. See p. 1016, Table 5. ↑
32. “Mothers were assessed at … 2 weeks postpartum and thereafter biweekly until the infant reached 6 months of age. … Assessors documented what the infant had been fed in the last 24 hours. This information was categorized as either EBF, partial breastfeeding … or no breastfeeding” (p. e426). ↑
33. “O presente estudo investigou, para ambos os grupos, as seguintes variáveis aos 6 meses de idade: aleitamento materno exclusivo, definido como o uso de aleitamento materno como único alimento oferecido à criança, sem oferta de chá e água; aleitamento materno, definido como a presença de leite materno na alimentação da criança, independente da oferta de qualquer outro alimento; medidas antropométricas e as variáveis sócio-demográficas” (p. 1450). In English: “The present study investigated, for both groups, the following variables at 6 months of age: exclusive breastfeeding, defined as the use of breastfeeding as the only food offered to the child, without offering tea and water; breastfeeding, defined as the presence of breast milk in the child’s diet, regardless of the offering of any other food; anthropometric measurements and sociodemographic variables.” ↑
34. See p. 881, Table 2. ↑
35. See p. 8, Table 2. ↑
36. Morrow et al. (1999) did not mention assessing non-exclusive breastfeeding in the protocol, which just says, “Infants were followed up until 3 months of age to assess exclusive breastfeeding and diarrhoea, and 6 months of age to assess duration of any breastfeeding” (p. 1227). However, the paper reports data on non-exclusive breastfeeding intensities on pp. 1228-1229 (see Table 4). ↑
37. “Breastfeeding status at the time of interview was recorded (24 h recall). The mother was then asked if she had fed her baby anything other than breastmilk since the last visit. If she had on 2 successive days or more, this information was taken into consideration when classifying feeding status. Thus, a baby at month 4 who had been exclusively breastfed in the past 24 hours, but had had 2 successive days of other milk or food during the month, would be classified as partly breastfed at month 4. If in the following month, the baby had been exclusively breastfed throughout, this would be classified as exclusively breastfed at month 5” (p. 1644). ↑
38. “Current breastfeeding was assessed at all scheduled postpartum visits with past 24-h and 7-day recalls” (p. 423). We reached out to Thorkild Tylleskär to confirm whether the study measured non-exclusive intensities but did not hear back. ↑
39. “We assessed … the prevalence of exclusive breastfeeding at 14 and 24 weeks post partum. WHO definitions and two timeframes (the past 24 h and past 7 days) were used for maternal recall of exclusive breastfeeding” (p. e549). ↑
40. “Primary outcomes included … infant feeding, namely exclusively breastfeeding during the first four months of life” (p. 117). ↑
41. “The primary outcome was the prevalence of EBF at 1, 3 and 6 months determined on 24 h recalls. The secondary outcome was cumulative (since birth) EBF determined at 6 months” (p. 1734). ↑
42. Diminishing intensity of intervention can be unintentional (see here). ↑
43. We are not clear what the Sinha review defines as continuation, as the study discusses “continued breastfeeding” as over 6 months on page 114, but as 12-23 months on page 116. ↑
44. Only the abstract appears to have been published. This study offers a comprehensive global trend analysis of breastfeeding rates and provides useful prevalence data broken down by type (exclusive, predominant, partial) and geography. Accessing the full article could help to gain more granular insights into regional variations and historical trends. ↑
45. This study includes geospatial maps of EBF prevalence in subnational regions of Africa. These maps could inform targeted intervention strategies in low-performing areas, and we recommend GiveWell look into them more closely for a better understanding of where to target. ↑
46. There appears to be an implicit assumption that morbidity reduction and mortality reduction are proportional, for any given cause. While this assumption seems tenuous to us, it seems reasonable enough, given the lack of high-quality evidence on mortality effects, so long as this assumption is consistently applied across similar contexts evaluated by GiveWell. ↑
47. Mortality in infants aged ≥1 year, diarrhea morbidity, respiratory infection morbidity, otitis media morbidity, maternal effects, birth spacing effects, savings from not purchasing baby formula, general adverse effects, skin-to-skin contact. ↑
48. The original assumption reads: “All infectious diseases and nutritional deficiencies are affected. X% reduction in mortality. Half of “other n[e]onatal disorders” are directly or indirectly related to infection (my very rough assumption), so these are reduced by X/2%.” ↑
49. In the actual cost-effectiveness analysis, “other neonatal disorders” and “neonatal preterm birth” are affected at 50% of the rate expected based on share of all-cause mortality, while “sudden infant death syndrome” is affected at 25% of the expected rate. ↑
50. We’re unsure how broadly these options apply to all water quality interventions. ↑
51. “Only enteric diseases are affected. X% reduction in enteric disease mortality.” ↑
52. The study is unclear about whether this is comparing EBF versus exclusive formula feeding or some other mix. ↑
53. We spent several days searching for high-quality studies on this subject, mostly attempting to restrict the context of this research to relatively recent studies in LMICs. We believe that further research is not likely to reveal many additional relevant publications on the matter. That said, it appears that an extensive literature in HICs supports public health organizations’ emphasis on EBF, but we have not prioritized such studies for this draft. One expert shared our impression that there isn’t “good empirical evidence to quantify the exact relationship.” ↑
54. The study also evaluated relative risks for “infection-related mortality,” including sepsis, meningitis, pneumonia, diarrhoea, measles, malaria, and more. Compared to EBF, predominant breastfeeding was associated with a 1.7-fold higher risk, partial breastfeeding with a 4.56-fold higher risk, and no breastfeeding with an 8.66-fold higher risk (Table 3, p. 9). ↑
55. Due in part to the heightened risk of social desirability bias inflating the true level of breastfeeding intensity in the treatment group compared to the control group. ↑
56. Based on Olufunlayo et al. (2019); see p. 13, Figure 2, which shows that every included study had an effect size on exclusive breastfeeding greater than 1, indicating an increase in the rate of exclusive breastfeeding. ↑
57. GiveWell’s replication excluded Tahir et al. (2012), as the study involved a telephone-based intervention. ↑
58. We refer to them as the treatment group below, although there were in fact multiple treatment arms. The relevant treatment group is also known as the “nutrition group.” ↑
59. We have not been able to find other copies of this graph, but based on the citation in the screenshot we believe it is originally from Nutrition for Developing Countries, a 1992 book by Felicity Savage King and Ann Burgess. ↑
60. Although this is also from maternal reports, we (and one of our interviewees) believe it is less susceptible to social desirability bias than breastfeeding behavior. ↑
61. Lantagne said that women living with HIV have a “small risk … that you can transmit HIV through breast milk,” describing this as “ethically one of the most difficult” problems in global health. We did not look into this further as the question of breastfeeding among women living with HIV is out of scope. ↑
62. It is not necessarily a problem that e.g., the assessments that placed people into these categories were not exactly the same in the two studies. But, if this led to objectively very different levels of breastfeeding being assigned to different categories across the different studies, then this would pose a further challenge to combining their outcomes together in a common analysis. ↑
63. i.e., the latent distribution underpinning the observed ordinal outcomes is modeled as a standard normal distribution ↑