Meta-analyses on charitable giving clarify evidence for empathic and effective altruism

Domain: biology
Published: 2026-03-10
Editorial outcome: accept

Abstract
Effective altruists argue that charitable giving is over-influenced by empathic responses and should
instead be guided by cost-benefit analyses about the effectiveness of giving. To provide insight into the
extent to which empathy and effectiveness are associated with charitable giving in the population, two
meta-analyses are conducted, synthesising 416 effect sizes from 124 papers sampling 74,797
participants. Here we show that effectiveness, r = .34, SE = .04, 95%CIs [.28, .40], and empathy, r =
.25, SE = .02, CIs [.21, .29], both positively relate to charitable giving overall. However, prediction
intervals reveal significant heterogeneity. Moderation analyses reveal one crucial caveat to the overall
association between effectiveness and charitable giving: although the mean effect is relatively large
when effectiveness is measured, r = .42, CIs [.35, .48], manipulated effectiveness has a weak effect, r =
.03, CIs [-.10, .17]. Our findings suggest that while people may self-perceive as effective altruists, they
give like empathic ones, a disjunction that calls for deeper causal investigation.

Introduction
Understanding why and to what extent people engage in charitable giving has long been a
preoccupation of social scientists.1 One reason for this is that charitable giving serves an important
function in sustaining a healthy and inclusive society. Estimated at over $470 billion per year in the U.S.
alone2, charitable giving funds help, care, and services in ways that cannot be readily substituted
through commercial or government activities. As such, charitable giving is designed to enrich lives, and
in many cases to save lives. Another reason charitable giving has preoccupied scholars is its symbolic
value in signifying the degree to which people engage in kindness and compassion to others.
Understanding charitable giving helps us understand who we are as humans, and how we express our
humanity.

One of the biggest debates about charitable giving – both within and outside academia – is
whether people rely too much on their “heart” when giving, and not enough on their “head”. In his book
Against Empathy3 – and in high-profile opinion pieces4 – Paul Bloom makes the case that empathy is a
poor moral guide to charitable giving. In line with the empathy-altruism hypothesis5,6, Bloom agrees
that empathy plays a role in activating the motivation to do good. However, it also leads us to make
ineffective or unfair charitable decisions, focusing on issues that respond to our immediate emotional
triggers rather than grounding our compassion in rational deliberation about which causes do most good
(i.e., effectiveness considerations). Consistent with this notion, effective altruism scholars propose
decision-making frameworks for judging how effective one’s giving will be such as “How many people
benefit, and by how much?” and “What are the chances of success?”7-9 Although earlier critiques
positioned empathy and effectiveness as competing motives, recent evidence suggests they may be
mutually reinforcing, particularly when empathic concern is broadened to include distant others and is
guided by reasoning about impact.10-13

To assess research on the association between charitable giving, effectiveness, and empathy, a
key distinction lies between studies that rely on self-reports of these constructs and studies that
experimentally manipulated them. While the debate about the role of empathy in charitable giving has
gained increasing attention in recent years, prior syntheses have excluded experimental designs, making
this comparison unclear. When it comes to effectiveness, this distinction becomes especially salient
given high-profile experiments suggesting that donors have relatively little appetite to seek out
information about welfare impact14, and that when it is provided effectiveness information has limited
impact on charitable giving15 and choice of charities16.

The goal of this paper is to add an important missing piece to the debate: meta-analyses of the
extent to which charitable responses are, in fact, associated with empathy and perceived effectiveness.
By combining the voices of thousands of participants sampled by hundreds of researchers across several
decades, one is in a stronger position to distinguish signal from noise when examining the associations
between charitable giving, empathy, and effectiveness. We emphasise that the goal of this paper is not
to compare empathy and effectiveness directly. There are too few studies that measure both constructs
within the same sample, and the fields from which these constructs originate use different
operationalisations. Instead, our aim is to provide a descriptive and independent synthesis of the extent
to which each construct is associated with charitable giving, and under what conditions.

Before doing so, some definitional clarification is required. Empathy is a multi-dimensional
construct, one that is often used interchangeably with constructs such as sympathy and compassion. A
particularly important distinction is made between “emotional empathy”, which Bloom refers to as
“feeling what you believe other people feel – experiencing what they experience” (p.3)3 and “cognitive
empathy”, which is variously referred to in the literature as social intelligence, theory of mind, and
perspective taking. In Against Empathy, Bloom makes it clear that his case is primarily about the limits
of affective empathy. So although we meta-analyse all operationalisations of empathy here, we note that
it is affective empathy that is most closely aligned to the debate that inspired the current paper. As
illustrated below, empathy has been operationalised in many different ways (e.g., cognitive versus
affective; dispositional versus situational; experimentally versus correlationally) and drilling down into
the patterns for each helps illuminate the different ways in which empathy may be associated with
charitable giving. Empirical synthesis is overdue: the first meta-analysis on the link between empathy
and prosocial behaviour was published nearly 40 years ago, and incorporated only a handful of studies
on charitable giving.17 Subsequent syntheses have not examined experimental work, focusing
exclusively on correlational links between measures of empathy and questionnaire measures of
dispositional pro-social behaviour18,19 or between measures of empathy and resource allocations in lab-
based games such as the Dictator Game and the Prison er’s Dilemma20.

In extracting data for the effectiveness meta-analysis, we excluded the related literature on
efficiency, that is, the proportion of money that goes to beneficiaries as opposed to being absorbed by
administrative costs.21,22 We made this decision in line with the arguments of effective altruism
advocates, who make it clear that the efficiency of a charity should not be a primary criterion for
judging whether it is effective (i.e., a charity for which 99.99% of income is funnelled directly towards a
pointless mission is efficient but not effective)7. Instead, we meta-analyse studies that measure or
manipulate variables sometimes referred to as “response efficacy”, “perceived donation efficacy”, or
“perceived impact of donation”: constructs that are measured through items such as “How much good
do you think you can do by donating money to this organisation?” or “To what extent do you think that
your donation would make a positive difference?”

Finally, we restricted our analysis to charitable giving, as distinct from other forms of prosocial
behaviour. We defined charitable giving as “voluntary contributions of money that benefit people
outside the giver’s family”.1 We had two reasons for restricting the analysis to charitable giving. First, it
is an operationalisation of giving that most closely aligns to the effective altruism movement, which is
best known for providing moral context around which charities to support financially. Second, by
restricting the range to one domain of prosocial behaviour, we reduce statistical noise and unwanted
heterogeneity associated with comparing effect sizes across different behaviours.23 Patterns of altruism
across domains (e.g., donating money versus blood versus time) are psychologically distinct24, so
focusing just on charitable giving leaves us in a better position to make like-for-like comparisons
between studies.

Here, we show through two meta-analyses that empathy is a robust correlate of charitable giving
and reliably increases generosity when experimentally evoked. Perceived effectiveness, on the other,
hand predicts giving strongly at the self-report level and weakly under experimental manipulation. We
conclude that people give like empathic altruists even when they see themselves as effective ones, a
pattern that sharpens the empirical context within which debates about effective altruism unfold.

Results
We followed the Preferred Reporting Items for Systematic Reviews and Meta-analyses
(PRISMA)25,26 to identify quantitative research on (1) the association between effectiveness and
charitable giving and (2) the association between empathy and charitable giving. PRISMA flowcharts,
summarising the screening process, are presented in Supplementary Figs. S1 and S2. Full reference lists
for papers included in the empathy and effectiveness meta-analyses are included in the Supplementary
file.

Pearson’s correlation (r) was used to represent the association between charitable giving and the
two variables of interest: effectiveness and empathy. To approximate a normal sampling distribution,
Pearson r correlations were transformed to Fisher’s z correlations for analyses. For ease of
interpretation, we report values transformed back to Pearson r correlations. Given that the majority of
articles included in both meta-analyses reported multiple dependent effect sizes, we employed a three-
level meta-analytic approach to calculate the overall effect size and perform moderator analyses. All
tests of significance are 2-tailed unless otherwise specified.

We examined publication bias in two ways: visual inspection of the Funnel Plots (where
asymmetry may indicate publication bias) and Egger’s Sandwich test, which was used given the
presence of dependent effect sizes. As can be seen in Fig. 1, no clear or systematic asymmetry is shown
for either meta-analysis. Consistent with visual inspection, Egger’s tests were non-significant for both
effectiveness (p = .260) and empathy (p = .804), indicating no statistical evidence of a pattern indicating
publication bias.

Heterogeneity and treatment of moderators.

We calculated I2 (the proportion of total variance in study results due to heterogeneity rather
than sampling error) which suggested a high degree of heterogeneity for both the effectiveness (96%)
and empathy (92%) meta-analysis. To determine if the within-paper variance (Level 2) and between-
paper variance (Level 3) were significant, two one-tailed log-likelihood-ratio tests were performed.
These tests compared the fit of the three-level model (which accounted for variance at Levels 2 and 3) to
the fit of a two-level model in which variance at only one of the levels was freely estimated. Significant
variance in effect sizes was observed at both the within-paper level (both ps < .001) and between-paper
level (both ps < .001). Using Cheung’s27 formula, 2.48% of the total variance in the association between
effectiveness and charitable giving, and 5.46% of the variance in the association between empathy and
charitable giving, was attributed to sampling variance. Considerably more variance is attributable to
within-paper variance (32.33% in the effectiveness analysis, 24.11% in the empathy meta-analysis) and
between-paper variance (65.19% for effectiveness, 70.43% for empathy). In addition to estimating the
overall effect size, we calculated the prediction interval for each meta-analysis. Prediction intervals
estimate the likely range of effect sizes that might be observed in future studies with similar
characteristics. The range of effect sizes was r = -.17 to r = .71 for effectiveness and r = -.14 and r = .57
for empathy. These heterogeneity tests indicate that the true effects vary significantly across papers and
measures, and that future studies on these associations may report correlations that vary widely.

Moderation analyses identify likely causes of this heterogeneity. To account for the potential
issue of multicollinearity, we followed Hox and colleagues’ recommendation to first test for the effect
of each potential moderator separately using univariate models.28 We then conducted multiple
moderator analyses on a single model that included all significant moderators identified in the univariate
analyses for each meta-analysis.

In the main body of this manuscript, we discuss moderators that are most relevant from a
theoretical and/or practical perspective. For the sake of thoroughness, however, we also ran ancillary
moderation analyses based on sample characteristics: the proportion of women in the sample; the
average age of participants; whether data were collected in Western, Educated, Industrialised, Rich, and
Democratic (WEIRD) or non-WEIRD countries29; whether the sample comprised students or non-
students; and whether the sample was collected using online or offline methods. These analyses are
reported in the bottom half of Tables 1 and 2. In short, none of these sampling characteristics were
statistically significant moderators of the association between effectiveness and charitable giving (all ps
> .35) or the association between empathy and charitable giving (all ps > .08) and so we do not
elaborate on these analyses further.

Effectiveness

Overall, a medium-sized positive association was found between effectiveness and charitable
giving, r = .34, p < .001, t = 9.85, 95% CIs[.28, .40]. However, as can be seen in Table 1, three
moderators significantly qualified this conclusion. First, the association was significantly stronger when
charitable giving was self-reported (e.g., willingness to donate, future intentions to donate, self-reported
past giving; r = .38, p < .001) than when studies used behavioural measures of giving (e.g., direct
observations of giving in the field, the amount of a study payment that the participant donated; r = .27, p
< .001). Second, the association was significantly stronger when participants reported their likelihood of
giving (r = .37, p < .001) compared to when participants reported a monetary value of giving (r = .29, p
< .001). Third, the association between effectiveness and charitable giving was only significant when
effectiveness was measured (r = .42, p < .001). When effectiveness was manipulated, the average effect
was trivial in size and statistically non-significant (r = .03, p = .612).

Finally, we examined whether the different operationalisations of effectiveness corresponded to
differences in strength of association. In the literature, the dominant operationalisation was what we
refer to here as donation effectiveness, a construct that is sometimes referred to as “response efficacy”,
“perceived donation efficacy”, or “perceived impact of donation”. What unites these operationalisations
is that they refer to the extent that the donation will be effective in achieving positive outcomes
(example item: “How much good do you think you can do by donating money to this organisation?”).
However, as can be seen in Table 1, at least three other operationalisations exist in the literature. What
we label as charity effectiveness refers to perceptions of the effectiveness of charities in general
(measured by items such as "Charitable organisations have been quite successful in helping the needy").
What we label as collective effectiveness refers to perceptions of the extent to which collectives can
make a difference (e.g., “I think together we can successfully change things in relation to this issue”)
whereas personal effectiveness refers to perceptions of whether participants can personally make a
difference (e.g., “I think it seems possible to make a big difference"). Regardless of how effectiveness
was operationalised, a significant and positive association was found, the strength of which did not
differ reliably across dimensions.

Following Hox and colleagues’ recommendations28, we extended the three-level meta-regression
model to simultaneously include the moderators identified to be significant in the univariate analyses
(i.e., measured vs manipulated, self-report vs behaviour, likelihood vs value). The multiple moderator
analysis was significant, F(3,150) = 15.51, p < .001, revealing a significant unique moderating effect of
measured vs manipulated effectiveness on the overall association between effectiveness and giving (see
Table 3 for number of effect sizes and statistical output).

Consistent with the univariate analyses, when effects of the other significant moderators were
taken into account, the association between effectiveness and charitable giving was again only
significant when effectiveness was measured (and not when effectiveness was manipulated). However,
the other moderators (self-report vs behaviour, likelihood vs value) were no longer significant. A
possible explanation is that these variables covaried with the measured versus manipulated distinction.
Specifically, experimental studies were more likely to employ behavioural outcomes (rather than self-
reports) and assess donation value (rather than likelihood), which may have suppressed the independent
contributions of these moderators in the full model. In this context, the available data make it difficult to
completely disentangle their unique effects within the multivariate analysis.

Empathy

Overall, a medium-sized positive association was found between empathy and charitable giving,
r = .25, p < .001, t = 11.55, 95% CIs[.21, .29]. Contrary to the pattern of the effectiveness meta-analysis,
there was no statistically significant difference in the strength of that association depending on whether
empathy was measured or manipulated (both rs = .25, both ps < .001; see Table 2). As in the
effectiveness meta-analysis, the association between empathy and charitable giving was significantly
stronger when giving was self-reported (r = .27, p < .001) than when studies used behavioural measures
of giving (r = .22, p < .001). The association was also significantly stronger when giving was measured
in terms of likelihood of giving (r = .29, p < .001) versus the monetary value that participants gave
(r=.21, p<.001). Moreover, a stronger association was found when empathy was operationalised
situationally (i.e., as a state variable; r = .27, p < .001) than when it was measured dispositionally (i.e.,
as a trait variable; r = .20, p < .001).

A final moderator was the dimension of empathy that was being captured. A common critique of
the field is that researchers’ use of the term “empathy” glosses over theoretically meaningful
distinctions. In our systematic review, the dominant operationalisation was what we label here as
emotional empathy, incorporating constructs united by a focus on emotion felt toward a group or
individual in need (variously described in the literature as “compassion”, “sympathy”, “empathic
concern”, or “affective empathy”). As can be seen in Table 2, the strongest association between
empathy and charitable giving emerged when empathy was operationalised this way (r = .27, p < .001).
Significantly weaker than this (but still significant; r = .20, p < .001) were effect sizes in studies in
which empathy was operationalised in a more cognitive way (e.g., as a form of perspective taking
toward a group or individual in need but without any reference to emotion). Finally, some studies
measured empathy as personal distress without explicitly linking that distress to a target group. Most of
these were drawn from studies using the personal distress sub-factor of the Interpersonal Reactivity
Index, which incorporates items such as “Being in a tense emotional situation scares me”.30 When
operationalised this way, empathy shared a relatively small association with charitable giving (r = .09, p
= .005), significantly weaker than for the other two dimensions.

We extended the three-level meta-regression model to simultaneously include the moderators
identified to be significant in the univariate analyses (i.e., state vs trait, dimension of empathy, self-
report vs behaviour, likelihood vs value). The multiple moderator analysis was significant, F(5,228) =
20.15, p < .001, revealing a significant unique moderating effect of state vs trait empathy, dimension of
empathy, and likelihood vs value on the overall association between empathy and giving (see Table 4
for number of effect sizes and statistical output).

When effects of the other significant moderators were accounted for, studies that measured state
empathy yielded a significantly stronger relation compared to studies that measured trait empathy.
Similarly, an identical pattern of findings to the univariate analyses emerged for the dimension of
empathy and likelihood vs value moderators: studies that measured emotional empathy and cognitive
empathy yielded a significantly stronger association than those that measured personal distress, and
studies that captured giving likelihood yielded a significantly stronger association compared to those
that captured giving value. In this model, however, the self-report vs behaviour moderator was no longer
significant.

Methods
Search strategy

Literature searches were initially run in November 2019 and the search was refreshed in
December 2022. The search was conducted across four databases: the two largest multidisciplinary
academic databases (Scopus and Web of Science) plus content-relevant databases in business
(ABI/Inform) and psychology (PsycINFO). For both libraries we used search terms nested around
charitable giving (donation*, donate, donor*, philanthrop*, charitable, "not for profit*", "non profit*",
nonprofit*, NGO*, "non governmental", “third sector” , "charit*") and the factor of interest:
effectiveness (“effective altruism”, “effective giving”, "donation effective*”, “charity effective*”,
“nonprofit effective*”, efficacy, competence, "impact of gift", "donation impact", “nonprofit impact”,
“charity impact”), and empathy (empath*, sympath*, compassion*). Searches were based on title,
abstract, and keywords. Results were supplemented through snowballing from reference lists and open
calls for unpublished data distributed through X and mailing lists of the Association for Research on
Nonprofit Organizations and Voluntary Action, American Marketing Association, and Society for
Personality and Social Psychology. To help identify relevant grey literature, we also screened the first
20 pages (200 results) in Google Scholar (consistent with standard practice)42 using the same search
terms identified in the database searching.

Inclusion criteria and screening

To be eligible for inclusion, studies needed to include a quantitative measure of charitable giving
(as part of correlational or experimental designs), be reported in English, and published 1980 or later.
Correlational studies allowed us to estimate the strength of naturalistic associations, while experimental
studies enabled us to examine causal effects of manipulating empathy or effectiveness on giving
behaviour. We excluded purely qualitative, theoretical, or descriptive studies because they do not
provide effect sizes or statistical associations necessary for meta-analysis. Similarly, we did not include
studies based on simulation models, ethnographic observation, or administrative records without direct
measurement of the psychological constructs of interest, as these designs do not allow for computation
of comparable quantitative associations.

In these meta-analyses, we coded for several moderators. In doing so, we defined intention
likelihood as a self-reported assessment of the likelihood or willingness to donate to a charitable cause
(e.g., “How likely are you to donate to this organisation?”). Value was defined as the monetary value
participants reported they would donate or actually donated. We distinguished between measured
giving, where donation behaviours or intentions were assessed without experimental manipulation of the
constructs of interest, and manipulated giving, where donation behaviours or intentions were measured
after an experimental manipulation aimed at influencing empathy or perceived effectiveness. Self-report
measures refer to participants’ stated responses to survey items about their donation intentions or
behaviour (e.g., likelihood of donating or intended donation amount), whereas behavioural measures
involve participants making actual donation decisions, typically involving real or incentivised financial
contributions.

There were no limits on age or nationality of participants. Papers that were not full-length
articles (e.g., book reviews, books, conference abstracts, corrections, legal judgements) were not
included. The second and third authors screened texts for eligibility on title and then again on abstract,
resolving discrepancies through discussion. Both screeners had experience conducting and publishing
meta-analyses previously. Screening on the full text was conducted by the second author. For articles
less than 10 years old that did not report bivariate effect sizes, we emailed authors to request this
information.

Analytic strategy

Following the screening process, data on the association between effectiveness and charitable
giving were analysed from 47 papers, comprising 81 independent samples and 157 effect sizes (N =
32,116). Data on the association between empathy and charitable giving were analysed from 77 papers,
comprising 105 independent samples and 259 effect sizes (N = 42,681). Where an experiment both
manipulated and measured effectiveness (for example as a manipulation check) both effect sizes were
included (one in the “manipulated” category and one in the “measured” category).

We employed a three-level meta-analytic approach to calculate the overall effect size and
perform moderator analyses. To determine the appropriate level at which to model statistical
dependence among effect sizes, we compared alternative multilevel random-effects structures and
modelled dependence at the paper level; model comparisons and sensitivity analyses are reported in the
OSF supplement. The total variance is partitioned into three components: sampling variance (Level 1),
within-paper variance reflecting dependence among studies in the same article (Level 2), and between-
paper variance (Level 3), thereby appropriately accounting for the clustering of effect sizes. To conduct
our analyses, we followed the procedures outlined by Assink and Wibbelink43 and used the rma.mv
function of the Metafor package44 in the R environment (version 4.4.0)45. We used a multilevel random
effects model, and restricted maximum likelihood estimation method to calculate all model parameters.
The t-distribution was used to test individual regression coefficients and for calculating confidence
intervals46.

The type of bivariate effect size extracted depended on study design, but we typically extracted
Pearson’s correlation coefficients (r) for correlational studies or Cohen’s ds for experimental studies. In
situations where these values were not provided by the study, we used test statistics (e.g., means and
standard deviations, F-values, frequency data) to calculate effect sizes. All effect sizes were transformed
to Pearson r correlations for the meta-analysis (see OSF for effect size conversion formulas).

A leave-one-out analysis did not identify any studies that influenced the overall findings. To
check for extreme effect sizes that may disproportionately influence the results, we screened for those
with standardised scores larger than 3.29 or smaller than 3.29.47 No outliers were identified in the
effectiveness meta-analysis, and only one outlier was identified in the empathy meta-analysis.
Regardless of whether this effect size was included or excluded, analyses yielded similar findings, so we
opted to include this effect size in all subsequent analyses.

Data availability statement

The data are publicly available on the Open Science Framework:
https://doi.org/10.17605/OSF.IO/QZ9AX. 48

Code availability statement

Analyses were conducted through R, using code that is viewable on the Open Science Framework:
https://doi.org/10.17605/OSF.IO/QZ9AX. 48

Peer review rounds
[{"round": 1, "reviewer_comments": {"reviewer_1": "In a meta analyses of 416 effect sizes from 74,797 participants, the authors examine the extent by which charitable giving is shaped by perceptions of effectiveness versus empathy. They find that self-reported effectiveness perceptions explain more variance in charitable giving than empathy, but effectiveness interventions do not reliably influence charitable giving. This is my first time reviewing this paper. I appreciated the opportunity to read this work. The key strength of the paper is the inclusion of two large-scale meta-analyses aggregating an impressive number of studies on charitable giving, which provide a nuanced perspective about the extent to which empathy and effectiveness perceptions motivate charitable giving and confirm rather paradoxical behaviors that people self-report in ways that imply effectiveness is very important to them, but seem relatively unmoved by actual effectiveness information. With reasonable updates, I think this work will be of interest to a broad readership. These are the things I suggest to help make the paper stronger: MAJOR COMMENTS Empathic Versus Effectiveness Debate The introduction—notably the 2nd, 3rd, and 4th paragraphs—set up a debate about “empathic” versus “effective” altruism, but then state that the “goal of this paper is not to weigh up the moral arguments of the effective altruism movement or the case against empathy” but to conduct “meta-analyses of the extent to which people are, in fact, influenced by effectiveness and empathy in making charitable decisions” (pg 3). This was quite striking to me for several reasons. First, Bloom’s arguments are not that people do not engage in empathic charitable giving, but that it may be unfair or less effective at actually helping. Second, and more importantly, much work over the last decade suggests that empathic and effective altruism are more compatible than previously argued (e.g., Everett et al., 2018; Fowler et al., 2021; Law et al., 2022, 2024). Setting up this debate in order to ask “to what extent does empathy or effectiveness drive charitable giving?” seems misleading and distracting from the main study. An alternative motivation might be best described by the authors in the Discussion, which focus on the following questions: Is charitable giving overly influenced by empathy? Is charitable giving under-influenced by analytical, cost-benefit analyses about maximising good? How successful is empathy induction in promoting charitable giving? How successful are effectiveness interventions in promoting charitable giving? Readers may benefit more by motivating your study from this perspective and providing additional background on evidence for the \"effectiveness paradox\" rather than the empathy versus effectiveness debate. Everett, J. A., Faber, N. S., Savulescu, J., & Crockett, M. J. (2018). The costs of being consequentialist: Social inference from instrumental harm and impartial beneficence. Journal of Experimental Social Psychology, 79, 200-216. Fowler, Z., Law, K. F., & Gaesser, B. (2021). Against empathy bias: The moral value of equitable empathy. Psychological Science, 32(5), 766-779. Law, K. F., Amormino, P., Marsh, A. A., & O’Connor, B. B. (2024). Ethical reasoning versus empathic bias: A false dichotomy? Trends in Cognitive Sciences, 28(1), 1–4. Law, K. F., Campbell, D., & Gaesser, B. (2022). Biased benevolence: The perceived morality of effective altruism across social distance. Personality and Social Psychology Bulletin, 48(3), 426-444. Statistical Models It appears that the authors run separate models for empathy and effectiveness and then qualitatively compare the effect sizes from each of the models to draw their conclusions (e.g., that perceived effectiveness predicts charitable giving over and above empathy). Is there a way to statistically compare these effect sizes directly? The authors might be limited by having no or few studies that measure both empathy and effectiveness (were there any that measured both?), but comparing effect sizes would immensely improve the inferences drawn by the results. If not, then this should be noted as a limitation. Other Forms of Altruism The authors focus on charitable giving, a well-studied and valid form of altruistic giving. How do they speculate their findings generalizing to other forms of altruism, such as stem cell donation or organ donation? Interestingly, the results show that self-reports of empathy are robustly associated with charitable giving. How do the authors reconcile these findings which recent work finding that self-reports of empathic concern are not robust predictors of other forms of real-world altruism (Rhoads et al., 2023)? Do the authors believe there is something specific about the relationship between empathic motivation and acts of charitable giving—perhaps the relative cost of charitable donations is lower or perhaps acts of charity are more outward forms of social or moral signaling linked to social desirability biases or norms? Rhoads, S. A., Vekaria, K. M., O’Connell, K., Elizabeth, H. S., Rand, D. G., Kozak Williams, M. N., & Marsh, A. A. (2023). Unselfish traits and social decision-making patterns characterize six populations of real-world extraordinary altruists. Nature Communications, 14(1), 1807. Describing the Included Studies The authors need a table either in main text or supporting information describing the specific measures used in each of the studies included their analyses and how they were classified. I did not see any description of this and thus it was difficult for me to interpret any of the results. For example, what does “Behavioural” mean in Table 2? Which behavioural measures of giving were used? This practice is fairly standard in meta-analysis papers. MINOR COMMENTS Perceived Effectiveness: I suggest the author stick with the term “perceived effectiveness” when discussing self-report effectiveness but describe it earlier. Typo on Line 205: “r = .??, p = .??” Lines 91-93: The authors state “the last meta-analysis on the link between empathy and prosocial behaviour was published over 35 years ago, and incorporated only a handful of studies on charitable giving.” However, meta-analytic studies have investigated the relationship between empathy and prosociality since Eisenberg & Miller (1987), notably: Thielmann, I., Spadaro, G., & Balliet, D. (2020). Personality and prosocial behavior: A theoretical framework and meta-analysis. Psychological Bulletin, 146(1), 30. I also found: Ding, F., & Lu, Z. (2016). Association between empathy and prosocial behavior: A systematic review and meta-analysis. Advances in Psychological Science, 24(8), 1159. Yin, Y., & Wang, Y. (2023). Is empathy associated with more prosocial behaviour? A meta‐analysis. Asian Journal of Social Psychology, 26(1), 3-22.", "reviewer_2": "The article's reports striking, original findings that make a crucial empirical contribution to the perennial debate about the nature of human altruism. The findings from experiments on charitable giving suggest that emotion drives charitable giving, whereas rational considerations about the donation's effectiveness are practically irrelevant to lay people's decisions of which charity to donate to. At the same time, the authors' meta-analysis of findings from correlational studies suggests that people might be deceiving themselves and/or others into thinking that the charities they donate to are more effective than those they didn't donate to. The article's findings significantly advance research on the psychology of (in)effective altruism, charitable giving, and several related fields. This is the first meta-analysis of research on the role of effectiveness considerations in charitable giving. To my knowledge, this is the first, authoritative direct comparison of the actual, causal effect of effectiveness considerations to people's post-hoc rationalizations of their decisions. This comparison revealed a crucial discrepancy between what people say and what people do. The methodology is sound, and the conclusions are well-supported by rigorous meta-analyses of the largest data set that has ever been brought to bear on these questions. The Methods section could benefit from additional information about how the effect sizes were computed for studies with experimental designs and how they were converted into r values. Relatedly, in Lines 197-200 of the Results section, the description of the difference between studies in which effectiveness was measured and studies in which it was manipulated should be more clear and more detailed. There is no reason why experiments that manipulate effectiveness couldn't also measure people's perceptions of effectiveness. It thus remains unclear whether the effects reported for experiments are associations between donations and experimentally induced perceptions of effectiveness or, as I assume, associations between the experimental manipulation and donations. This should be clarified. There also appears to be a rendering error in Lines 204-205 (\"r=.??, p=.??\"). I think adding information about how the effect sizes were computed for different study designs will be crucial to make the findings reproducible. In the interest of reproducibility, I think the authors should also release the data extracted from the articles, the scripts used to compute effect sizes from that information, and the computed effect sizes. I think the authors should also report confidence intervals on the reported effect size estimates. Explicit statistical comparisons between the effects of effectiveness and empathy would also be informative.", "reviewer_3": "Hi, I don’t have to much to say about this paper. My one main concern is it isn’t so obvious how to interpret this exercise. That is, it seems quite conceivable to me that efficiency perceptions/manipulations could be strongly/weakly correlated with giving behavior in laboratory experiments, even if they do/don’t correlate with real world giving behavior. Likewise, it is not clear to me that could compare the effects in the efficiency literature to the effects in the empathy literature to conclude that empathy is more or less significant for real world giving. It could just be, for instance, that the variation/manipulations in one of these literatures are particularly weak or strong, compared to the variation/manipulations real world charities use. Perhaps also efficiency matters more in some contexts rather than others, e.g. when side by side comparisons are possible or norms specify concern for efficiency? In which case, again, it is not clear how much we can learn from the r squared in experiments where the contexts may quite different from the real world. Perhaps the authors can speak to these issues a bit more?", "reviewer_4": "This paper reports the results of a meta-analysis exploring the relationships between perceived effectiveness and empathy with charitable giving. This is certainly a worthwhile and interesting project, and I appreciate the effort that goes into a meta-analysis. My evaluation of the research itself (the methods and reporting of the results) is mostly positive. But I do have somewhat large concerns regarding the framing of the research question and interpretation of the results. 1. The authors confuse “effectiveness” with “perceived effectiveness” throughout the manuscript. The meta-analysis only looks at perceived effectiveness and not actual effectiveness. Consequently, the results do not shed light on whether people are “effective altruists”. Presumably, many effective altruists would agree that perceived effectiveness differs starkly from actual effectiveness (and possibly that empathy itself may be correlated with (mis)perceived effectiveness). This is precisely why they think their cold calculations are needed to estimate effectiveness--because human intuition cannot be trusted. I thus think the introductory material and the conclusions/discussion surrounding effective altruism are mostly irrelevant to the current project. More generally, I think the introduction and general discussion should be rewritten to be more appropriate for the present meta-analysis, which I explain more below. 2. The authors overinterpret the importance of the difference between correlational and experimental results. A lack of experimental evidence does not mean there is no causal relationship. Experimental tests are one way to estimate causal relationships, but a failure to find them does not disprove them. The discussion of a “paradox” is thus unwarranted based on the current data. Any one manipulation might fail for countless reasons (e.g., people already have entrenched beliefs that cannot be changed with a 5 minute manipulation). The correlational results suggest that perceived effectiveness may be an important predictor of charitable giving. The conclusions should call for more research on the potential causal relationship rather than asserting it has been ruled out. 3. Relatedly, claims comparing the relative evidence for “empathy” vs. “effectiveness” seem unwarranted. First, the authors do not statistically test for differences between the effectiveness and empathy explanations. Second, it is inappropriate to disregard the correlation between perceived effectiveness and charitable giving in this comparison. Third, perceived effectiveness and empathy might be positively related. If the data are available, it would be helpful to report (1) the meta-analyzed associations between perceived effectiveness and empathy, and (2) the meta-analyzed manipulation checks for the empathy and effectiveness manipulations (so we know whether those manipulations were successful, how large the manipulation effects were, and whether they were equally successful). 4. The authors acknowledge that they cannot comment on arguments for or against “effective altruism” or for or against “against empathy”, yet these are the primary focuses of the abstract, introduction, and much of the discussion. I agree that the present project does not speak much to these movements/arguments. These data do not tell us whether people are (or should be) effective altruists, only that perceived effectiveness is related to charitable giving. And these data do not tell us whether people have too much or too little empathy, only that empathy appears to be a contributing factor to charitable giving. I thus think the framing of the paper as a potential challenge to those perspectives is inappropriate. A more neutral and accurate framing of the paper would be a simple focus on its own contribution—testing the extents to which empathy and perceived effectiveness relate to charitable giving. 5. Relatedly, in my view, the tone of the paper seems inappropriate for a science paper. The paper seems to lament that other scholars have received attention for their work in this space. The paper would have a more scientific tone if the introduction simply explained what was known to date and set up the open questions. Additionally, the paper should avoid exaggerating the conclusiveness of the results (e.g., “provide an authoritative answer…”). Scientific conclusions are generally tentative, not definitive. 6. The authors submitted their paper with some internal comments still visible. This raised concerns regarding transparency and awareness of their own data. For example, one internal comment stated “We originally had 31 but dropped the 2 “local” effects. We also had two missing effect sizes last time, but I’m presuming that these were included in the 31 count even though the effect sizes weren’t included in the calculations?” What does this mean? Why were effects dropped? What are the results with and without them? And why would two missing effect sizes be included in the reported number of effect sizes? 7. Additionally, this sentence was included with missing information: “After removing this effect size, a significant (but still modest) positive relationship emerged (r = .??, p = .??).” The r and p values should be added. 8. I was puzzled by this statement: “It should be noted that 1 of the 29 effect sizes was based on a very large sample (>11,000) and so had an out-sized influence on the overall mean effect.” The authors claim to have used a random effects model, in which case the effect sizes would not be weighted by sample size. Is there an explanation for this? 9. If the authors would like to comment on the potential effectiveness of effective-altruism-like interventions, they should separately report the results of the 22 studies that taught participants about effective altruism (and also resolve the internal disagreement among co-authors [seen in their tracked comments] about which studies fit this criterion). 10. The internal comments regarding this sentence are also concerning: “On the upside, over 80% of the effect sizes were drawn from non-student samples, and 32% measured actual donation behaviour as opposed to an intention or some other proxy of behaviour.” One co-author commented on how these calculations might be wrong, and the other commented that they were never done in the first place. 11. The abstract should report the number of included papers and studies in addition to effect sizes and total n. Despite these many issues, I do think the meta-analysis itself could be of interest to many people, including scholars interested in the effective altruism movement. I hope my comments will help the authors avoid likely criticisms of the current version of the manuscript.", "reviewer_5": "Thank you for the opportunity to review this manuscript. While the topic is important, the manuscript needs greater detail in the methods section. Below are methodological issues that need to be clarified. The abstract and manuscript itself imply that the meta-analysis results can answer a causal question, namely whether perceptions of effectiveness and empathy cause greater charitable giving. The word “shaped” implies causal inference, however meta-analyses are secondary studies and cannot make causal inferences. In addition, the synthesis includes a mix of studies, some correlational/observational and others reporting on experiments. The inclusion of both types of studies limits the review’s ability to discuss whether primary studies have established a causal relationship between perceptions of effectiveness and empathy. The abstract provides the average correlation between given and both effectiveness and empathy but does not provide the standard error of this estimate or the amount of heterogeneity present. The average correlation is important information, but it is equally important to understand how much variation exists across studies. The abstract needs to include both the standard error for the mean effect size to assess whether the correlation is significantly different from zero, and a measure of the heterogeneity across studies. See below for more discussion of the reporting of heterogeneity in this review. There is a mismatch between the aims of the paper and the types of studies included. Page 4, line 65 of the manuscript states that “the goal of this paper is to add an important missing piece to the debate: meta-analyses of the extent to which people are, in fact, influenced by effectiveness and empathy in making charitable decisions.” It appears that both correlational and experimental studies were included in this review. Only experimental studies that manipulate effectiveness and empathy can provide a direct estimate of the causal relationship between effectiveness and empathy and giving. The correlational studies can only examine the association between giving and perceived effectiveness and empathy. These two types of studies are addressing different research questions. It is unclear the nature of the studies included in this review, and how they address the key aim of the review. The search and screening methods need more detail. Searching. The manuscript reports examples of search terms but best practice is to include the exact search strings used for each database and the dates each search was carried out on each database. This information is often reported in the appendix. The review should include an Inclusion Criteria section describing in detail the population studied, all included study designs and outcomes. A rationale for the types of study designs should also be provided; the nature of the study designs included is unclear as described above. All of the included definitions of donation effectiveness and empathy should be described in this section. Additionally, definitions of constructs such as giving intention, amount of charitable giving., manipulated given and measured giving should be provided. The English language and publication date specifications will also be included in the Inclusion Criteria section as will any limitations on countries of origin. Screening. It is unclear in the manuscript how many screeners were used for each stage of the screening process. A double-screening process is standard practice to guard against any bias in this stage. This section should also report the process by which the authors determined the eligibility of each study and the order in which each item was addressed for both the title and abstract screening and full-text review. If a screening guide was used, include it in the appendix. This section should also describe the screeners and the training or preparation (i.e. pilot screening, etc.) they received. The 2015 Haddaway guidelines have been updated with more recent evidence. Google Scholar is no longer a recommended search system for evidence synthesis, because the searches are not reproducible. For more information, see the citation below. Gusenbauer, M. and Haddaway, N.R. (2019). Which academic search systems are suitable for systematic reviews or meta-analysis? Evaluating retrieval qualities of Google Scholar, PubMed, and 26 other resources. Research Synthesis Methods. DOI: 10.1002/jrsm.1378 Unpublished literature included in the review is limited to Google Scholar searches. The authors might consider refreshing their unpublished research search by searching dissertation and thesis databases or websites of related organizations. The coding process and included items is unclear. A coding section describes the process used to extract data from studies. Each item coded should be described either in narrative form or by providing the codebook. The coding section reports the number of coders, their experience levels, and any training they received including pilot coding. It is also unclear if the review included any critical appraisal/rating of study quality of the included studies. It is unclear how effect sizes were coded in the review. It is unclear how effect sizes were coded in this review. The review reports correlations, but experimental studies may provide information that would typically be synthesized in the form of a standardized mean difference or a mean difference if studies used the same outcome measure. It is unclear if standardized mean differences were converted to correlations, and what conversion formula was used. In addition, it is unclear how effect sizes were computed from correlation studies. It is unclear if the review limited the effect sizes to reported bivariate correlations or if bivariate correlations were estimated from other statistics such as regression coefficients. The section on publication bias indicates that only published studies were used in exploring potential selection bias. It is unclear why only published articles were used in the analyses exploring the potential impact of selection bias in this review. Publication bias concerns whether the overall estimates have the potential of bias due to small sample effects; deleting the unpublished studies provides an incomplete view of the evidence base. The review should use Egger’s sandwich test given the presence of dependent effect sizes. The manuscript reports three different tests for publication bias, but these tests are inappropriate when there are multiple effect sizes nested within studies. Egger’s sandwich tests funnel plot symmetry with dependent effect sizes. Please see the following reference for more information. Rodgers, M. A., & Pustejovsky, J. E. (2021). Evaluating meta-analytic methods to detect selective reporting in the presence of dependent effect sizes. Psychological Methods, 26(2), 141–160. https://doi.org/10.1037/met0000300 The manuscript should discuss heterogeneity in more detail. Page 8 of the manuscript describes the relative amount of variation at each level but does not provide the overall estimate of heterogeneity. The manuscript should report the within-study and between-study variance components for the model and use these components to report the prediction interval for the two main correlations. It is unclear how much studies vary in their estimates of the two key correlations. See below for a reference about reporting the prediction interval: Borenstein, M., Higgins, J. P. T., Hedges, L. V., & Rothstein, H. R. (2017). Basics of meta-analysis: I2 is not an absolute measure of heterogeneity. Research Synthesis Methods, 8(1), 5–18. https://doi.org/10.1002/jrsm.1230 Consider using meta-regression to analyze moderators. Table 1 appears to report single-variable moderator analysis. The limitation of this approach is that it is unclear how the moderators used in Table 1 relate to one another. With 259 effect sizes, the analysis can use multiple meta-regression with multiple moderators in a single model. Meta-regression can also accommodate both continuous and categorical in a single model. See the reference below for best practice in meta-regression: Tipton, E., Pustejovsky, J. E., & Ahmadi, H. (2019). A history of meta-regression: Technical, conceptual, and practical developments between 1974 and 2018. Research Synthesis Methods, 2(10), 161–179. https://doi.org/10.1002/jrsm.1338 Editing comments. The manuscript contained authors’ comments to each other On page 9, line 205, there is “??” where a number was intended. Terri Pigott, PhD, Georgia State University with the assistance of Natalie Pruitt, MS, Georgia State University"}, "author_response": "RESPONSE TO REVIEWERS We thank the five reviewers for your patience in receiving this revision; critical re-analyses had to wait for the 2nd author to return from maternity leave. In response to your very helpful suggestions, we have made several revisions. Most notably, we have remodelled the Introduction, included more details about our searching and screening processes, conducted several new analyses, and expanded the discussion. Below, we describe in detail how we have responded to each of your comments. In light of these changes, we believe the paper now makes a clearer, stronger and more focused contribution. We thank you for the time you have put into facilitating these improvements. Best regards, The authors REVIEWER 1 In a meta analyses of 416 effect sizes from 74,797 participants, the authors examine the extent by which charitable giving is shaped by perceptions of effectiveness versus empathy. They find that self-reported effectiveness perceptions explain more variance in charitable giving than empathy, but effectiveness interventions do not reliably influence charitable giving. This is my first time reviewing this paper. I appreciated the opportunity to read this work. The key strength of the paper is the inclusion of two large-scale meta-analyses aggregating an impressive number of studies on charitable giving, which provide a nuanced perspective about the extent to which empathy and effectiveness perceptions motivate charitable giving and confirm rather paradoxical behaviors that people self-report in ways that imply effectiveness is very important to them, but seem relatively unmoved by actual effectiveness information. With reasonable updates, I think this work will be of interest to a broad readership. These are the things I suggest to help make the paper stronger: We thank Reviewer 1 for their thoughtful and constructive advice. The introduction—notably the 2nd, 3rd, and 4th paragraphs—set up a debate about “empathic” versus “effective” altruism, but then state that the “goal of this paper is not to weigh up the moral arguments of the effective altruism movement or the case against empathy” but to conduct “meta-analyses of the extent to which people are, in fact, influenced by effectiveness and empathy in making charitable decisions” (pg 3). This was quite striking to me for several reasons. First, Bloom’s arguments are not that people do not engage in empathic charitable giving, but that it may be unfair or less effective at actually helping. Second, and more importantly, much work over the last decade suggests 2 that empathic and effective altruism are more compatible than previously argued (e.g., Everett et al., 2018; Fowler et al., 2021; Law et al., 2022, 2024). Setting up this debate in order to ask “to what extent does empathy or effectiveness drive charitable giving?” seems misleading and distracting from the main study. An alternative motivation might be best described by the authors in the Discussion, which focus on the following questions: Is charitable giving overly influenced by empathy? Is charitable giving under-influenced by analytical, cost-benefit analyses about maximising good? How successful is empathy induction in promoting charitable giving? How successful are effectiveness interventions in promoting charitable giving? Readers may benefit more by motivating your study from this perspective and providing additional background on evidence for the \"effectiveness paradox\" rather than the empathy versus effectiveness debate. Everett, J. A., Faber, N. S., Savulescu, J., & Crockett, M. J. (2018). The costs of being consequentialist: Social inference from instrumental harm and impartial beneficence. Journal of Experimental Social Psychology, 79, 200-216. Fowler, Z., Law, K. F., & Gaesser, B. (2021). Against empathy bias: The moral value of equitable empathy. Psychological Science, 32(5), 766-779. Law, K. F., Amormino, P., Marsh, A. A., & O’Connor, B. B. (2024). Ethical reasoning versus empathic bias: A false dichotomy? Trends in Cognitive Sciences, 28(1), 1–4. Law, K. F., Campbell, D., & Gaesser, B. (2022). Biased benevolence: The perceived morality of effective altruism across social distance. Personality and Social Psychology Bulletin, 48(3), 426-444. We thank Reviewer 1 for pushing us on this point. In light of these comments, as well as related comments from other reviewers, we have remodelled the Introduction. The 2nd, 3rd and 4th paragraphs highlighted above have been collapsed into one paragraph, deleting much of the previous discussion of the philosophical origins and cultural currency of the effective altruism movement. This provides a more focused introduction to our key questions. We also appreciate the opportunity to incorporate Reviewer 1’s suggested references into the paper. Together, these studies argue that empathy is not inherently narrow or biased (Fowler et al., 2021); people value impartial altruism when not paired with harm (Everett et al., 2018); effective altruism can be viewed as competent and moral, even when directed toward strangers (Law et al., 2022); and the notion that empathy and effectiveness are psychologically opposed is a false dichotomy (Law et al., 2024). We have added a sentence to the re-modelled Introduction to reflect this more integrative perspective: “Although some of these earlier critiques positioned empathy and effectiveness as competing motives, recent evidence suggests they may be mutually reinforcing—particularly when empathic concern is broadened to include distant others and is guided by reasoning about impact (Everett et al., 2018; Fowler et al., 2021; Law et al., 2022, 2024).” It appears that the authors run separate models for empathy and effectiveness and then qualitatively compare the effect sizes from each of the models to draw their conclusions (e.g., that perceived effectiveness predicts charitable giving over and above empathy). Is there a way to statistically compare these effect sizes directly? The authors might be limited by having no or few studies that measure both empathy and effectiveness (were there any that measured both?), but comparing effect sizes would immensely improve the inferences drawn by the results. If not, then this should be noted as a limitation. 3 This comment applied to the following passage in the Discussion of the original manuscript: “Correlationally, effectiveness ratings are considerably bigger predictors of charitable giving than empathy, explaining more than three times the variance (17% versus 5%). If one were to focus just on the correlational evidence, then, one might reach the conclusion that Bloom’s thesis in Against Empathy was alarmist: people’s charitable giving is in fact associated with judgements about effectiveness, and much more so than it is with empathy.” We agree with Reviewer 1: statements that the meta-analytic effect for effectiveness is bigger than that for empathy are inappropriate in the absence of formal significance tests. As Reviewer 1 anticipated, however, we are restricted here by the fact that only 9 studies measured both empathy and effectiveness, making a formal meta-regression test under-powered. A z-test for comparing two independent effect sizes confirmed that the correlational effect of effectiveness was indeed bigger than the correlational effect for empathy (z = -2.01, p = .044) but this test assumes that the two sets of studies are non-overlapping. We re-calculated the z-test removing the overlapping studies, and the result was exactly the same, but the deletion of effect sizes from the corpus is not ideal. After much discussion within the team, we could find no elegant way of walking the reader through all this. Given this statistical quandary, we decided to simply rephrase the above passage so as not to imply that we are formally comparing the size of the two effects (which is also more in keeping with the revised frame described above). We would like to keep the description of variance explained though, which we think is sufficient to tell the story of the data. Revised text: “When people self-report the effectiveness of a charity or charitable act, it has a medium-to-large association with giving (r = .42). In other words, perceptions of effectiveness explain approximately 17% of variance in charitable giving (to benchmark this, empathy explained only 5%).” The authors focus on charitable giving, a well-studied and valid form of altruistic giving. How do they speculate their findings generalizing to other forms of altruism, such as stem cell donation or organ donation? Interestingly, the results show that self-reports of empathy are robustly associated with charitable giving. How do the authors reconcile these findings which recent work finding that self-reports of empathic concern are not robust predictors of other forms of real-world altruism (Rhoads et al., 2023)? Do the authors believe there is something specific about the relationship between empathic motivation and acts of charitable giving—perhaps the relative cost of charitable donations is lower or perhaps acts of charity are more outward forms of social or moral signaling linked to social desirability biases or norms? Rhoads, S. A., Vekaria, K. M., O’Connell, K., Elizabeth, H. S., Rand, D. G., Kozak Williams, M. N., & Marsh, A. A. (2023). Unselfish traits and social decision-making patterns characterize six populations of real-world extraordinary altruists. Nature Communications, 14(1), 1807. We thank the reviewer for this thoughtful question. In response we have added the following paragraph to the Discussion: “Although charitable giving is a valid and well-studied expression of altruism, it is only one form among many. It remains an open question whether the patterns we observe here generalise to other forms of altruism that carry higher personal costs, such as organ donation, 4 stem cell registration, or direct physical aid. For instance, Rhoads and colleagues found that self-reported empathic concern was not a consistent predictor of real-world extraordinary altruism in these domains across six populations of altruistic individuals. Charitable giving may be more strongly influenced by empathy because it is (a) low-cost, (b) normatively endorsed, and (c) easily enacted. Additionally, some other forms of prosocial behaviour (e.g., volunteering, organ donation, sperm donation) provide more direct payoffs to the “giver” and so may be less empathically motivated. We encourage future research to test whether the role of empathy in charitable giving is driven by these contextual features, and to explore whether different psychological profiles underlie high-cost versus low-cost altruism.” The authors need a table either in main text or supporting information describing the specific measures used in each of the studies included their analyses and how they were classified. I did not see any description of this and thus it was difficult for me to interpret any of the results. For example, what does “Behavioural” mean in Table 2? Which behavioural measures of giving were used? This practice is fairly standard in meta-analysis papers. In the revision we point readers to the excel spreadsheet of the dataset on OSF. This spreadsheet contains written notes on specific measures used and how they were subsequently classified into the levels of the moderators. We have also added some brief written clarification in the manuscript itself at the first mention of the behavioural vs self-report distinction: “First, the association was significantly stronger when charitable giving was self-reported (e.g., willingness to donate, future intentions to donate, self-reported past giving; r = .38, p < .001) than when studies used behavioural measures of giving (e.g., direct observations of giving in the field, the amount of a study payment that the participant donated; r = .27, p < .001).” Perceived Effectiveness: I suggest the author stick with the term “perceived effectiveness” when discussing self-report effectiveness but describe it earlier. Throughout the manuscript, we refer to “perceived effectiveness” when referring to the correlational effects. Typo on Line 205: “r = .??, p = .??” Apologies for the embarrassing oversight. This and other minor glitches are due to the fact that we submitted the next-to-last version of the manuscript rather than the final version. A reminder of the context here: 1 of the 29 effect sizes was based on a very large sample (>11,000) and so the first author wanted to check whether it had an out-sized influence on the overall mean effect. When we saw that the meta-analytic effect size barely changed, it was pointed out by the second author that we used a random effects model and so the effect sizes were not weighted by sample size (a point made also by Reviewer 4). For this reason, this passage was deleted in the “final” draft (that was accidentally not submitted) and is deleted also from our revised version. Lines 91-93: The authors state “the last meta-analysis on the link between empathy and prosocial behaviour was published over 35 years ago, and incorporated only a handful of studies on charitable giving.” However, meta-analytic studies have investigated the relationship between empathy and prosociality since Eisenberg & Miller (1987), notably: Thielmann, I., Spadaro, G., & Balliet, D. (2020). Personality and prosocial behavior: A 5 theoretical framework and meta-analysis. Psychological Bulletin, 146(1), 30. I also found: Ding, F., & Lu, Z. (2016). Association between empathy and prosocial behavior: A systematic review and meta-analysis. Advances in Psychological Science, 24(8), 1159. Yin, Y., & Wang, Y. (2023). Is empathy associated with more prosocial behaviour? A meta‐analysis. Asian Journal of Social Psychology, 26(1), 3-22. We thank Reviewer 1 for directing us to this research, which we now acknowledge in the revised manuscript: “Empirical synthesis is overdue: the first meta-analysis on the link between empathy and prosocial behaviour was published nearly 40 years ago and incorporated only a handful of studies on charitable giving (Eisenberg & Miller, 1987). Subsequent syntheses have not examined experimental work, focusing exclusively on correlational links between measures of empathy and questionnaire measures of dispositional pro-social behaviour (Ding & Lu, 2016; Yin & Wang, 2023) or between measures of empathy and resource allocations in lab-based games such as the Dictator Game and the Prisoner’s Dilemma (Thielmann et al., 2020).” To elaborate on the three new references that have been included: The meta-analyses reported by Ding and Lu (2016) and Yin and Wang (2023) focus only on correlational research. Specifically, they examined only papers that measured empathy (dispositionally) and also measured pro-social behaviour as a dispositional trait (using scales such as Prosocial Behaviour Questionnaire, Prosocial Motivation Scale, Prosocialness Scale for Adults, Prosocial Tendencies Measure, Prosocial Tendencies Measure, and so forth). In both cases the meta-analyses only included papers that reported bivariate correlations. Where regressions were reported, the authors of these meta-analyses did not contact the authors of the original studies to obtain correlations; the study was simply left out of the meta-analysis. The Thielmann et al. (2020) meta-analysis was much more rigorous but focused only on personality dimensions (of which one was empathy, construed as a sub-facet of HEXACO) and their correlation with decisions made in 6 games: Dictator Game, Ultimatum Game, Trust Game, Prisoner’s Dilemma, Public Goods Game, Commons Dilemma. Given this – and mindful of the fact that there has been no meta-analysis on effectiveness at all – we think the claim “empirical synthesis is overdue” is warranted. REVIEWER 2 The article's reports striking, original findings that make a crucial empirical contribution to the perennial debate about the nature of human altruism. The findings from experiments on charitable giving suggest that emotion drives charitable giving, whereas rational considerations about the donation's effectiveness are practically irrelevant to lay people's decisions of which charity to donate to. At the same time, the authors' meta-analysis of findings from correlational studies suggests that people might be deceiving themselves and/or others into thinking that the charities they donate to are more effective than those they didn't donate to. The article's findings significantly advance research on the psychology of (in)effective altruism, charitable giving, and several related fields. This is the first meta-analysis of research on the role of effectiveness considerations in charitable giving. To my knowledge, this is the first, authoritative direct comparison of the actual, causal effect of effectiveness considerations to people's post-hoc rationalizations of their decisions. This comparison revealed a crucial discrepancy between what people say and what people do. The methodology is sound, and the conclusions are well-supported by rigorous meta-analyses of the largest data set that has ever been brought to bear on these questions. We thank Reviewer 2 for their supportive words and constructive advice below. The Methods section could benefit from additional information about how the effect sizes were computed for studies with experimental designs and how they were converted into r values. We have now elaborated on this in the Method section: “The type of bivariate effect size extracted depended on study design, but we typically extracted Pearson’s correlation coefficients (r) for correlational studies or Cohen’s ds for experimental studies. In situations where these values were not provided by the study, we used test statistics (e.g., means and standard deviations, F-values, frequency data) to calculate effect sizes. All effect sizes were transformed to Pearson r correlations for the meta-analysis (see OSF for effect size conversion formulas).” Relatedly, in Lines 197-200 of the Results section, the description of the difference between studies in which effectiveness was measured and studies in which it was manipulated should be more clear and more detailed. There is no reason why experiments that manipulate effectiveness couldn't also measure people's perceptions of effectiveness. It thus remains unclear whether the effects rported for experiments are associations between donations and experimentally induced perceptions of effectiveness or, as I assume, associations between the experimental manipulation and donations. This should be clarified. Yes, as Reviewer 2 assumed, the effects reported for experiments are associations between the experimental manipulation and donations. Where an experiment both manipulated and measured effectiveness (for example as a manipulation check) both effect sizes were included (one in the “manipulated” category and one in the “measured” category). We now clarify this in the Method section of the revised manuscript. There also appears to be a rendering error in Lines 204-205 (\"r=.??, p=.??\"). Apologies for the embarrassing oversight. This and other minor glitches are due to the fact that we submitted the next-to-last version of the manuscript rather than the final version. A reminder of the context here: 1 of the 29 effect sizes was based on a very large sample (>11,000) and so the first author wanted to check whether it had an out-sized influence on the overall mean effect. When we saw that the meta-analytic effect size barely changed, it was pointed out by the second author that we used a random effects model and so the effect sizes were not weighted by sample size (a point made also by Reviewer 4). For this reason, this passage was deleted in the “final” draft (that was accidentally not submitted) and is deleted also from our revised version. I think adding information about how the effect sizes were computed for different study designs will be crucial to make the findings reproducible. In the interest of reproducibility, I think the authors should also release the data extracted from the articles, the scripts used to compute effect sizes from that information, and the computed effect sizes. We have now included a Data Availability statement, making it clear that the results spreadsheets are available on the Open Science Framework, and a Code Availability statement, making it clear that the code underpinning the analyses is also available on OSF: https://osf.io/qz9ax/?view_only=fe8cf97778554e5ca343cbd23cf9fd9f I think the authors should also report confidence intervals on the reported effect size estimates. Confidence intervals for all simple effects are provided in Tables 1 and 2. Where overall effect sizes are described in text, we now include the confidence intervals. Explicit statistical comparisons between the effects of effectiveness and empathy would also be informative. As we noted in response to a similar comment from Reviewer 1, we are restricted here by the fact that only 9 studies measured both empathy and effectiveness, making a formal meta-regression test under-powered. A z-test for comparing two independent effect sizes confirmed that the correlational effect of effectiveness was indeed bigger than the correlational effect for empathy (z = -2.01, p = .044) but this test assumes that the two sets of studies are non-overlapping. We re-calculated the z-test removing the overlapping studies, and the result was exactly the same, but the deletion of effect sizes from the corpus is not ideal. After much discussion within the team, we could find no elegant way of walking the reader through all this. Given this statistical quandary, we decided to simply rephrase the above passage so as not to imply that we are formally comparing the size of the two effects (which is also more in keeping with the revised frame recommended by Reviewer 1 and Reviewer 4). REVIEWER 3 I don’t have to much to say about this paper. My one main concern is it isn’t so obvious how to interpret this exercise. That is, it seems quite conceivable to me that efficiency perceptions/manipulations could be strongly/weakly correlated with giving behavior in laboratory experiments, even if they do/don’t correlate with real world giving behavior. Likewise, it is not clear to me that could compare the effects in the efficiency literature to the effects in the empathy literature to conclude that empathy is more or less significant for real world giving. It could just be, for instance, that the variation/manipulations in one of these literatures are particularly weak or strong, compared to the variation/manipulations real world charities use. Perhaps also efficiency matters more in some contexts rather than others, e.g. when side by side comparisons are possible or norms specify concern for efficiency? In which case, again, it is not clear how much we can learn from the r squared in experiments where the contexts may quite different from the real world. Perhaps the authors can speak to these issues a bit more? Thank you for raising this important point. As noted above, we have rephrased passages in the Abstract, Introduction and Discussion to avoid the implication that we are formally comparing the size of the effects of empathy versus effectiveness (which is also more in keeping with the revised frame recommended by other reviewers). We also agree that interpreting cross-construct comparisons and extrapolating laboratory findings to real-world giving contexts must be done with caution. We now discuss these possibilities more explicitly in the revised Discussion section: “We re-emphasise that meta-analytic syntheses cannot make a definitive statement about whether instruction about effectiveness can have a causal influence on charitable giving. Failure to detect experimental effects does not equate to disproof of causality, and experimental null results can arise from numerous factors (e.g., manipulation weakness, psychological reactance, entrenched priors). Weak experimental effects may also be due to contextual features such as the absence of side-by-side comparisons, variation in donor norms, or limited ecological validity in some lab paradigms. Rather than ruling out an influence of information about effectiveness, the data highlight a tension in the literature: despite robust correlational evidence suggesting that perceived effectiveness predicts giving, experimental attempts to shift perceptions of effectiveness frequently fail to influence donation behaviour. This is a pattern that raises questions rather than one that resolves them, and we call for more nuanced and ecologically valid experimental work to explore potential causal pathways (e.g., longer-term, field-based interventions, or studies that leverage existing variation in perceived effectiveness). Future research should also explore how different dimensions of study quality (e.g., ecological validity, risk of bias, design strength, attrition) may affect conclusions in this area. In sum, our effect sizes and R² values should not be treated as literal estimates of variance explained in real-world contexts, but rather as indicators of the extent to which these constructs are currently leveraged successfully in both correlational and experimental work. This distinction highlights the current limits of effectiveness-based interventions and the need for more ecologically valid research in this domain.” REVIEWER 4 This paper reports the results of a meta-analysis exploring the relationships between perceived effectiveness and empathy with charitable giving. This is certainly a worthwhile and interesting project, and I appreciate the effort that goes into a meta-analysis. My evaluation of the research itself (the methods and reporting of the results) is mostly positive. But I do have somewhat large concerns regarding the framing of the research question and interpretation of the results. We thank Reviewer 4 for the time and care they have taken suggesting improvements to our manuscript. 1. The authors confuse “effectiveness” with “perceived effectiveness” throughout the manuscript. The meta-analysis only looks at perceived effectiveness and not actual effectiveness. Consequently, the results do not shed light on whether people are “effective altruists”. Presumably, many effective altruists would agree that perceived effectiveness differs starkly from actual effectiveness (and possibly that empathy itself may be correlated with (mis)perceived effectiveness). This is precisely why they think their cold calculations are needed to estimate effectiveness--because human intuition cannot be trusted. I thus think the introductory material and the conclusions/discussion surrounding effective altruism are mostly irrelevant to the current project. More generally, I think the introduction and general discussion should be rewritten to be more appropriate for the present meta-analysis, which I explain more below. We agree with Reviewer 4 that we are not in a position to assess actual effectiveness. Rather, our paper meta-analyses (1) perceived effectiveness (in the correlational work) and (2) information about actual effectiveness (in the experimental work). Throughout the manuscript, we now refer to “perceived effectiveness” when referring to the correlational effects. In line with Reviewer 4’s suggestion, we have also remodelled the Introduction to reduce the focus on effective altruism as a movement (three paragraphs dedicated to this in the original manuscript have been condensed into one paragraph). On reflection, we agree that the focus on the underlying philosophy of effective altruism is a distraction that sets up a misleading expectation about what the manuscript actually achieves, which is to examine the association between perceived effectiveness and charitable giving, and between manipulated effectiveness and charitable giving. 2. The authors overinterpret the importance of the difference between correlational and experimental results. A lack of experimental evidence does not mean there is no causal relationship. Experimental tests are one way to estimate causal relationships, but a failure to find them does not disprove them. The discussion of a “paradox” is thus unwarranted based on the current data. Any one manipulation might fail for countless reasons (e.g., people already have entrenched beliefs that cannot be changed with a 5 minute manipulation). The correlational results suggest that perceived effectiveness may be an important predictor of charitable giving. The conclusions should call for more research on the potential causal relationship rather than asserting it has been ruled out. We appreciate the reviewer’s thoughtful caution regarding the interpretation of our findings, particularly the distinction between causal inference and experimental manipulation. We agree that a failure to detect experimental effects does not equate to disproof of causality, and that experimental null results can arise from numerous factors (e.g., manipulation weakness, psychological reactance, entrenched priors). We now acknowledge these points more explicitly in the revised Discussion: “We re-emphasise that meta-analytic syntheses cannot make a definitive statement about whether instruction about effectiveness can have a causal influence on charitable giving. Failure to detect experimental effects does not equate to disproof of causality, and experimental null results can arise from numerous factors (e.g., manipulation weakness, psychological reactance, entrenched priors). Weak experimental effects may also be due to contextual features such as the absence of side-by-side comparisons, variation in donor norms, or limited ecological validity in some lab paradigms. Rather than ruling out an influence of information about effectiveness, the data highlight a tension in the literature: despite robust correlational evidence suggesting that perceived effectiveness predicts giving, experimental attempts to shift perceptions of effectiveness frequently fail to influence donation behaviour. This is a pattern that raises questions rather than one that resolves them, and we call for more nuanced and ecologically valid experimental work to explore potential causal pathways (e.g., longer-term, field-based interventions, or studies that leverage existing variation in perceived effectiveness). Future research should also explore how different dimensions of study quality (e.g., ecological validity, risk of bias, design strength, attrition) may affect conclusions in this area. In sum, our effect sizes and R² values should not be treated as literal estimates of variance explained in real-world contexts, but rather as indicators of the extent to which these constructs are currently leveraged successfully in both correlational and experimental work. This distinction highlights the current limits of effectiveness-based interventions and the need for more ecologically valid research in this domain.” At the same time, we would like to clarify the intent behind our use of the term “effectiveness paradox.” Our goal was not to assert that causal influence has been definitively ruled out, but rather to highlight a tension in the literature: despite robust correlational evidence suggesting that perceived effectiveness predicts giving, experimental attempts to shift perceptions of effectiveness have generally failed to influence donation responses. We now take care to frame this as a pattern that raises questions rather than one that resolves them, and we explicitly call for more nuanced and ecologically valid experimental work to explore the potential causal pathways (e.g., longer-term, field-based interventions, or studies that leverage existing variation in perceived effectiveness). Our goal is not to assert that one construct is more “important” in an absolute sense, but to identify where the empirical evidence is stronger or weaker in predicting charitable responses under current research paradigms. We now make this framing more explicit in the Discussion. In short, we have revised the manuscript to (a) temper any language that implies causality has been ruled out, (b) avoid overinterpreting experimental nulls, and (c) recast the “paradox” language as an invitation for further investigation rather than a definitive conclusion. 3. Relatedly, claims comparing the relative evidence for “empathy” vs. “effectiveness” seem unwarranted. First, the authors do not statistically test for differences between the effectiveness and empathy explanations. Second, it is inappropriate to disregard the correlation between perceived effectiveness and charitable giving in this comparison. Third, perceived effectiveness and empathy might be positively related. If the data are available, it would be helpful to report (1) the meta-analyzed associations between perceived effectiveness and empathy, and (2) the meta-analyzed manipulation checks for the empathy and effectiveness manipulations (so we know whether those manipulations were successful, how large the manipulation effects were, and whether they were equally successful). We agree with Reviewer 4 that statements that the meta-analytic effect for effectiveness is bigger than that for empathy are inappropriate in the absence of formal significance tests. As discussed in response to similar comments from Reviewers 1 and 2, we are restricted by the fact that only 9 studies measured both empathy and effectiveness, making a formal meta-regression test under-powered. A z-test for comparing two independent effect sizes confirmed that the correlational effect of effectiveness was indeed bigger than the correlational effect for empathy (z = -2.01, p = .044) but this test assumes that the two sets of studies are non-overlapping. We re-calculated the z-test removing the overlapping studies, and the result was exactly the same, but the deletion of effect sizes from the corpus is not ideal. After much discussion within the team, we could find no elegant way of walking the reader through all this. Given this statistical quandary, we decided to simply rephrase the above passage so as not to imply that we are formally comparing the size of the two effects (which is also more in keeping with the revised frame recommended by Reviewer 1 and in point 4 below). In response to the last point, we conducted ancillary meta-analyses for the manipulation checks. Overall, these meta-analyses showed that the empathy manipulation checks were significantly associated with empathy, r = .29, t = 3.02, p = .014,95% CIs [.08, .48], and that the effectiveness manipulation checks were significantly associated with effectiveness, r = .43, t = 3.79, p = .009,95% CIs [.16, .64]. However, we note a significant caveat to the latter finding: many experimental studies did not have a fit-for-purpose manipulation check and so the latter effect is built on just 7 effect sizes. For this reason, we have not included these data in the revised manuscript but stand ready to do so if the editor / reviewers feel it adds value. 4. The authors acknowledge that they cannot comment on arguments for or against “effective altruism” or for or against “against empathy”, yet these are the primary focuses of the abstract, introduction, and much of the discussion. I agree that the present project does not speak much to these movements/arguments. These data do not tell us whether people are (or should be) effective altruists, only that perceived effectiveness is related to charitable giving. And these data do not tell us whether people have too much or too little empathy, only that empathy appears to be a contributing factor to charitable giving. I thus think the framing of the paper as a potential challenge to those perspectives is inappropriate. A more neutral and accurate framing of the paper would be a simple focus on its own contribution—testing the extents to which empathy and perceived effectiveness relate to charitable giving. As mentioned above, we agree that the focus on the underlying philosophy of effective altruism is a distraction that sets up a misleading expectation about what the manuscript actually achieves, which is to examine the association between perceived effectiveness and charitable giving, and between manipulated effectiveness and charitable giving. In the revision, we have reworked the opening paragraphs to reduce discussion of the effective altruism movement and to provide a more focussed and accurate framing of the paper. As an aside, we never intended the manuscript to be “a potential challenge” to the “effective altruism” or “against empathy” perspectives. Indeed, we see our data as sympathetic to both these perspectives. If the tone of the paper implied otherwise, that is our fault. For example, the last sentence of the original Abstract read “In sum, meta-analyses reveal more evidence for empathic altruism than for effective altruism”. What we intended by this was that there is more evidence that people are influenced by information about empathy (i.e., they are behaving like “empathic altruists”) than by information about effectiveness (i.e., they are not behaving like “effective altruists”). This is one of the key points being made by the scholars we cite in the Introduction such as Bloom, MacAskill, Ord and Singer: people give with their heart more than their head. We understand that this sentence could be misconstrued, however, and so we deleted it from the revised Abstract. With fresh eyes we can also see how the original title could have given this impression (“Meta-analyses reveal more evidence for empathic altruism than for effective altruism”). This is why, in the revision, we have reworked the title to read “Meta-analyses show robust evidence that people are empathic altruists, and tenuous evidence that they are effective altruists”. 5. Relatedly, in my view, the tone of the paper seems inappropriate for a science paper. The paper seems to lament that other scholars have received attention for their work in this space. The paper would have a more scientific tone if the introduction simply explained what was known to date and set up the open questions. Additionally, the paper should avoid exaggerating the conclusiveness of the results (e.g., “provide an authoritative answer…”). Scientific conclusions are generally tentative, not definitive. We thank the reviewer for this important feedback on tone. Our intention was not to lament others’ contributions, but rather to situate our work within an already highly visible and influential public and academic debate. That said, we appreciate that some of the wording may have inadvertently read as overly editorial, and we have revised the relevant sections to adopt a more neutral and scientific tone. Specifically, we now place greater emphasis on outlining what is known, what remains unknown, and why the current meta-analysis contributes to resolving open empirical questions. We also appreciate the concern about overstating the conclusiveness of the findings. Phrases such as “provide an authoritative answer” have been revised to reflect the tentativeness and evolving nature of scientific knowledge. We now use more appropriately cautious language (e.g., “sheds light on the current state of evidence”) in the manuscript. Thank you again for prompting these improvements; we believe the revised version is now more in line with the tone and framing expected in empirical scientific papers. 6. The authors submitted their paper with some internal comments still visible. This raised concerns regarding transparency and awareness of their own data. For example, one internal comment stated “We originally had 31 but dropped the 2 “local” effects. We also had two missing effect sizes last time, but I’m presuming that these were included in the 31 count even though the effect sizes weren’t included in the calculations?” What does this mean? Why were effects dropped? What are the results with and without them? And why would two missing effect sizes be included in the reported number of effect sizes? The comment boxes are due to the fact that we submitted the next-to-last version of the manuscript rather than the final version. Some context here: when it became clear that the null result of effectiveness manipulations was a headline finding, the author team met to go through each effect size one-by-one, to make sure they belonged in the analysis and were not under-estimating the meta-analytic result (essentially a team audit of the data). In that discussion we decided to drop two effect sizes that a skeptical reader could perceive to be an unfair test of the power of effectiveness to promote charitable giving. Both of these effect sizes were part of a somewhat complex study in which the authors manipulated effectiveness at the same time as they manipulated whether the charity was local or international (the “local” effects referred to in the comment). The wording of the stimuli made the local versus international manipulation much more salient than the effectiveness information, and the manipulation occurred simultaneously, making it difficult to disentangle the unique effect of effectiveness. On balance, we decided that this may have helped explain the null results of effectiveness in that study, and so the analysis would be more rigorous if we dropped these effect sizes. We note that the meta-analytic correlation for manipulations of effectiveness was almost identical regardless of whether these effect sizes were included or excluded (.034 v/ .036). In our audit we also discovered two effect sizes that had passed the selection and screening process but for which the relevant effect sizes had not been transcribed into the data sheet (the “missing” effects referred to in the comment). Although none of these changes affected the headline finding, we acknowledge that these oversights were unfortunate. However, we were pleased that the quality assurance processes within the team picked up the mistakes prior to submission. 7. Additionally, this sentence was included with missing information: “After removing this effect size, a significant (but still modest) positive relationship emerged (r = .??, p = .??).” The r and p values should be added. 8. I was puzzled by this statement: “It should be noted that 1 of the 29 effect sizes was based on a very large sample (>11,000) and so had an out-sized influence on the overall mean effect.” The authors claim to have used a random effects model, in which case the effect sizes would not be weighted by sample size. Is there an explanation for this? Points 7 and 8 are an unfortunate legacy of the fact that the very final draft of the manuscript was not the one submitted. In line with point 6 above, this analysis was part of a process we went through to ensure that the null result of manipulated effectiveness on charitable giving was reliable and not an artifact. In this case, because 1 of the 29 effect sizes was based on a very large sample (>11,000) the first author wanted to check whether it had an out-sized influence on the overall mean effect. When we saw that the meta-analytic effect size barely changed, it was pointed out by the second author that we used a random effects model and so the effect sizes were not weighted by sample size (the same point as Reviewer 4’s point 8). For this reason, this passage was deleted in the “final” draft (that was accidentally not submitted) and is deleted also from our revised version. 9. If the authors would like to comment on the potential effectiveness of effective-altruism-like interventions, they should separately report the results of the 22 studies that taught participants about effective altruism (and also resolve the internal disagreement among co-authors [seen in their tracked comments] about which studies fit this criterion). In line with Reviewer 4’s suggestion, we have conducted a posthoc meta-analysis of the effect sizes in which participants were taught about effective altruism. The meta-analysis of just these effect sizes revealed a larger overall effect (r = .10) although this was still non-significant, t = 1.24, p = .230, 95% CIs [-.07, .27]. This is now reported in the Discussion. As outlined above, internal disagreements about the number of studies that satisfied this criterion were resolved prior to the original submission. 10. The internal comments regarding this sentence are also concerning: “On the upside, over 80% of the effect sizes were drawn from non-student samples, and 32% measured actual donation behaviour as opposed to an intention or some other proxy of behaviour.” One co-author commented on how these calculations might be wrong, and the other commented that they were never done in the first place. This is another legacy of the fact that the second-to-last draft of the manuscript was the version submitted. In this case, we knew we were going to do this analysis, so the first author put in a back-of-the-envelope calculation as a placeholder in the manuscript. The second author put in the correct figures – which are the figures the reviewers saw – but the comment was still visible. Again, we apologise for the oversight but confirm that the numbers that were seen by reviewers remain the correct numbers. 11. The abstract should report the number of included papers and studies in addition to effect sizes and total n. We have now revised the abstract to include number of papers, effect sizes, and total N. Despite these many issues, I do think the meta-analysis itself could be of interest to many people, including scholars interested in the effective altruism movement. I hope my comments will help the authors avoid likely criticisms of the current version of the manuscript. We thank Reviewer 4 for their supportive words and excellent feedback. REVIEWER 5 Thank you for the opportunity to review this manuscript. While the topic is important, the manuscript needs greater detail in the methods section. Below are methodological issues that need to be clarified. The abstract and manuscript itself imply that the meta-analysis results can answer a causal question, namely whether perceptions of effectiveness and empathy cause greater charitable giving. The word “shaped” implies causal inference, however meta-analyses are secondary studies and cannot make causal inferences. In addition, the synthesis includes a mix of studies, some correlational/observational and others reporting on experiments. The inclusion of both types of studies limits the review’s ability to discuss whether primary studies have established a causal relationship between perceptions of effectiveness and empathy. We thank Reviewer 5 for pointing this out. We have now gone through the manuscript to avoid causal language, particularly when discussing the overall effect sizes and the effect sizes for the correlational research. The abstract provides the average correlation between given and both effectiveness and empathy but does not provide the standard error of this estimate or the amount of heterogeneity present. The average correlation is important information, but it is equally important to understand how much variation exists across studies. The abstract needs to include both the standard error for the mean effect size to assess whether the correlation is significantly different from zero, and a measure of the heterogeneity across studies. We have now revised the abstract to include standard errors and confidence intervals to better capture heterogeneity. There is a mismatch between the aims of the paper and the types of studies included. Page 4, line 65 of the manuscript states that “the goal of this paper is to add an important missing piece to the debate: meta-analyses of the extent to which people are, in fact, influenced by effectiveness and empathy in making charitable decisions.” It appears that both correlational and experimental studies were included in this review. Only experimental studies that manipulate effectiveness and empathy can provide a direct estimate of the causal relationship between effectiveness and empathy and giving. The correlational studies can only examine the association between giving and perceived effectiveness and empathy. These two types of studies are addressing different research questions. It is unclear the nature of the studies included in this review, and how they address the key aim of the review. We have now gone through the manuscript to avoid causal language, particularly when discussing the overall effect sizes and the effect sizes for the correlational research. We have also revised the statement in the Introduction about the goal of the paper. Although the experimental studies do speak to this question, we agree that this is a misleading way to summarise the goals of the project as a whole, which includes both experimental and correlational studies. The search and screening methods need more detail. Searching. The manuscript reports examples of search terms but best practice is to include the exact search strings used for each database and the dates each search was carried out on each database. In line with this recommendation, the search strings and dates for each database are now included in the OSF (https://osf.io/qz9ax/?view_only=fe8cf97778554e5ca343cbd23cf9fd9f) The review should include an Inclusion Criteria section describing in detail the population studied, all included study designs and outcomes. A rationale for the types of study designs should also be provided; the nature of the study designs included is unclear as described above. All of the included definitions of donation effectiveness and empathy should be described in this section. Additionally, definitions of constructs such as giving intention, amount of charitable giving., manipulated given and measured giving should be provided. Thanks for pointing out this oversight. In the revision we have now included Inclusion Criteria as a discrete sub-heading in the Method section. Here, we provide the details asked for above, including a rationale for the types of study designs included. When describing the moderators we now make it clearer what we mean by constructs such as giving intention, amount of charitable giving, manipulated giving, and measured giving.Detail about how individual studies were coded can be found in the. We note that we spent paragraphs 4-6 in the Introduction defining empathy, effectiveness, and charitable giving. Different dimensions of both empathy and effectiveness were also defined in the results, so to avoid redundancy we did not repeat this definitional work in the Method. The English language and publication date specifications will also be included in the Inclusion Criteria section as will any limitations on countries of origin. English language and publication date specifications are provided in the new Inclusion Criteria section in the Method. There were no limitations on countries of origin. Screening. It is unclear in the manuscript how many screeners were used for each stage of the screening process. A double-screening process is standard practice to guard against any bias in this stage. This section should also report the process by which the authors determined the eligibility of each study and the order in which each item was addressed for both the title and abstract screening and full-text review. If a screening guide was used, include it in the appendix. This section should also describe the screeners and the training or preparation (i.e. pilot screening, etc.) they received. The second and third authors screened texts for eligibility on title and then again on abstract, resolving discrepancies through discussion. Both screeners had experience conducting and publishing meta-analyses previously. Screening of the full text was conducted by the second author. The 2015 Haddaway guidelines have been updated with more recent evidence. Google Scholar is no longer a recommended search system for evidence synthesis, because the searches are not reproducible. For more information, see the citation below. Gusenbauer, M. and Haddaway, N.R. (2019). Which academic search systems are suitable for systematic reviews or meta-analysis? Evaluating retrieval qualities of Google Scholar, PubMed, and 26 other resources. Research Synthesis Methods. DOI: 10.1002/jrsm.1378 Unpublished literature included in the review is limited to Google Scholar searches. The authors might consider refreshing their unpublished research search by searching dissertation and thesis databases or websites of related organizations. We clarify that the unpublished literature included in the review was not limited to Google Scholar searches. In the manuscript we write “Results [of searches] were later supplemented through snowballing from reference lists and open calls for unpublished data distributed through X and mailing lists of the Association for Research on Nonprofit Organizations and Voluntary Action, American Marketing Association, and Society for Personality and Social Psychology. To help identify relevant grey literature, we also screened the first 20 pages (200 results) in Google Scholar using the same search terms identified in the database searching.” We are aware of the critique that Google Scholar searches may not be replicable over time or across machines. However, we kept Google Scholar searches as part of a repertoire of strategies for screening for unpublished research because it indexes many kinds of documents not found in traditional academic databases (e.g., working papers, reports, conference proceedings) and because it includes a wider range of disciplines, including less mainstream or region-specific sources, which may be useful in interdisciplinary or global topics. The coding process and included items is unclear. A coding section describes the process used to extract data from studies. Each item coded should be described either in narrative form or by providing the codebook. The coding section reports the number of coders, their experience levels, and any training they received including pilot coding. It is also unclear if the review included any critical appraisal/rating of study quality of the included studies. The coded dataset is available to reviewers on the OSF link, and this will be made publicly available should the manuscript be accepted for publication. We appreciate the reviewer raising the issue of study quality assessment. In this meta-analysis, we did not conduct a formal critical appraisal or quality rating of each study. Our dataset included a mix of experimental and correlational studies, which would have made consistent quality coding challenging in the absence of field-standard tools. Unlike in medicine, where tools like the Cochrane Risk of Bias tool exist, there's no universally accepted scale for appraising study quality in behavioural or psychological meta-analyses—especially when mixing experimental and correlational studies. Instead, we aimed to capture patterns of association across the full breadth of the literature, and sought to statistically address heterogeneity and potential quality-related concerns through rigorous moderator analyses (e.g., self-report vs behavioural measures; published vs unpublished data; likelihood vs value outcomes etc.). That said, we acknowledge that the absence of formal quality appraisal may limit the extent to which readers can assess the robustness of individual studies. We now mention this as a limitation in the Discussion and encourage future research to explore how different dimensions of study quality (e.g., risk of bias, design strength, attrition) may affect conclusions in this area. It is unclear how effect sizes were coded in the review. It is unclear how effect sizes were coded in this review. The review reports correlations, but experimental studies may provide information that would typically be synthesized in the form of a standardized mean difference or a mean difference if studies used the same outcome measure. It is unclear if standardized mean differences were converted to correlations, and what conversion formula was used. In addition, it is unclear how effect sizes were computed from correlation studies. It is unclear if the review limited the effect sizes to reported bivariate correlations or if bivariate correlations were estimated from other statistics such as regression coefficients. We have now elaborated on this in the Method section: “The type of bivariate effect size extracted depended on study design, but we typically extracted Pearson’s correlation coefficients (r) for correlational studies or Cohen’s ds for experimental studies. In situations where these values were not provided by the study, we used test statistics (e.g., means and standard deviations, F-values, frequency data) to calculate effect sizes. All effect sizes were transformed to Pearson r correlations for the meta-analysis (see OSF for effect size conversion formulas).” The section on publication bias indicates that only published studies were used in exploring potential selection bias. It is unclear why only published articles were used in the analyses exploring the potential impact of selection bias in this review. Publication bias concerns whether the overall estimates have the potential of bias due to small sample effects; deleting the unpublished studies provides an incomplete view of the evidence base. The review should use Egger’s sandwich test given the presence of dependent effect sizes. The manuscript reports three different tests for publication bias, but these tests are inappropriate when there are multiple effect sizes nested within studies. Egger’s sandwich tests funnel plot symmetry with dependent effect sizes. Please see the following reference for more information. Rodgers, M. A., & Pustejovsky, J. E. (2021). Evaluating meta-analytic methods to detect selective reporting in the presence of dependent effect sizes. Psychological Methods, 26(2), 141–160. https://doi.org/10.1037/met0000300 The goal of our original publication bias tests was to assess whether studies which tend to show positive, or statistically significant results are more likely to be published, compared to those with negative or null findings. Effect sizes from unpublished studies were not included as it was our understanding that doing so would hinder our ability to detect this bias, and may distort the overall effect size by underestimating the true effect. We conducted these tests on the aggregated effect sizes from each study using methods for conventional meta-analysis as we were unsure consensus had been reached on appropriate methods for detecting bias in the presence of dependent effect sizes. Thank you for bringing Egger’s sandwich test to our attention. We have now revised our analyses accordingly and retained the unpublished studies for the Egger’s Sandwich test (see text below): “We examined publication bias in two ways: visual inspection of the Funnel Plots (where asymmetry on the left and right side may indicate publication bias) and Egger’s Sandwich test (where a significant statistic indicates publication bias). Egger’s Sandwich test was used given the presence of dependent effect sizes. As can be seen in Figure 3, an asymmetrical spread of effect sizes is shown for both effectiveness and empathy. Consistent with visual inspection, the results of the Egger’s test revealed significant asymmetry in the funnel plots for both effectiveness (p = .010) and empathy (p < .001), suggesting publication bias is likely.” The manuscript should discuss heterogeneity in more detail. Page 8 of the manuscript describes the relative amount of variation at each level but does not provide the overall estimate of heterogeneity. The manuscript should report the within-study and between-study variance components for the model and use these components to report the prediction interval for the two main correlations. It is unclear how much studies vary in their estimates of the two key correlations. See below for a reference about reporting the prediction interval: Borenstein, M., Higgins, J. P. T., Hedges, L. V., & Rothstein, H. R. (2017). Basics of meta-analysis: I2 is not an absolute measure of heterogeneity. Research Synthesis Methods, 8(1), 5–18. https://doi.org/10.1002/jrsm.1230 We now provide more details on heterogeneity in the main text, including reporting I2 and the prediction interval for the two main correlations (see Heterogeneity and treatment of moderators section): “First, we calculated I2 (the proportion of total variance in study results that was due to heterogeneity rather than sampling error) which suggested a high degree of heterogeneity for both the effectiveness (96%) and empathy (92%) meta-analysis. Second, to determine if the within-study variance (Level 2) and between-study variance (Level 3) were significant, two one-tailed log-likelihood-ratio tests were performed. These tests compared the fit of the three-level model (which accounted for variance at Levels 2 and 3) to the fit of a two-level model in which variance at only one of the levels was freely estimated. Significant variance in effect sizes was observed at both the within-study level (both ps < .001) and between-study level (both ps < .001). Using Cheung’s formula, we found that 2.48% of the total variance in the association between effectiveness and charitable giving could be attributed to sampling variance, 32.33% to within-study variance, and 65.19% to between-study variance. Similarly, 5.46% of the total variance in the association between empathy and charitable giving could be attributed to sampling variance, 24.11% to within-study variance, and 70.43% to between-study variance. Third, in addition to estimating the overall effect size, we calculated the prediction interval for each meta-analysis. The prediction interval takes into account both the within-study and between-study variance to estimate the likely range of effect sizes that might be observed in future studies with similar characteristics. The range of effect sizes was r = -.17 to r = .71 for effectiveness and r = -.14 and r = .57 for empathy. Results of these heterogeneity tests indicate that the true effects vary significantly across studies and measures, and that future studies on these associations may report correlations that vary widely.” Consider using meta-regression to analyze moderators. Table 1 appears to report single-variable moderator analysis. The limitation of this approach is that it is unclear how the moderators used in Table 1 relate to one another. With 259 effect sizes, the analysis can use multiple meta-regression with multiple moderators in a single model. Meta-regression can also accommodate both continuous and categorical in a single model. See the reference below for best practice in meta-regression: Tipton, E., Pustejovsky, J. E., & Ahmadi, H. (2019). A history of meta-regression: Technical, conceptual, and practical developments between 1974 and 2018. Research Synthesis Methods, 2(10), 161–179. https://doi.org/10.1002/jrsm.1338 We thank Reviewer 5 for pressing us on this important point. In the revision, for each meta-analysis, we now have a section titled “multiple moderator analysis” in which we conduct meta-regressions with all the significant moderators in a single model. Results of these analyses – which do not change the take-home findings – can be found on pp. 9-11. Editing comments. The manuscript contained authors’ comments to each other On page 9, line 205, there is “??” where a number was intended. We apologise for the oversights. This and other minor glitches are due to the fact that we accidentally submitted the next-to-last version of the manuscript rather than the final version. As noted above, all of the internal discussions visible in comments were resolved prior to submission – so the data are valid – but the comments were simply not deleted. As discussed above, the missing numbers on the original line 205 were part of a passage that has now been deleted. Thank you Prof. Pigott and Dr. Pruitt for the excellent feedback. 1 RESPONSE TO REVIEWER COMMENTS Reviewer #1: This is my second review of this manuscript. I appreciate the opportunity to review. I also appreciate the authors’ comprehensive revisions, especially given the large number of reviewers. I believe the paper and analyses are much stronger. The identified “effectiveness paradox” is quite fascinating and will be of broad interest. We thank Reviewer 1 for the supportive feedback and for their help improving the manuscript in previous rounds. I have a few remaining comments that I hope can be addressed before publication. I appreciate the authors’ revision of the text re: Qualitative comparison of variance explained by effectiveness versus empathy. As the authors note, there is unfortunately no elegant approach to statistically compare the effect sizes of the effectiveness effects and the empathy effects because the authors run separate models for empathy and effectiveness and there are few studies that measure both empathy and effectiveness. Yet, the authors still include this comparison (pg. 12): “perceptions of effectiveness explain approximately 17% of variance in charitable giving (to benchmark this, empathy explained only 5%)”. Is variance explained by empathy an appropriate benchmark, here? We have now deleted the sentence in which we compared the variance explained. More importantly, I believe the authors should explicitly state that effectiveness and empathy are not being compared, and why, in the Introduction (perhaps the third paragraph?). We now include the following text in the revised paragraph 3: “We emphasise that the goal of this paper is not to compare empathy and effectiveness directly. There are too few studies that measure both constructs within the same sample, and the fields from which these constructs originate use different operationalisations. Instead, our aim is to provide a descriptive and independent synthesis of the extent to which each construct is associated with charitable giving, and under what conditions.” I also believe mentioning this as a study limitation in discussion may be an important call for future studies to formally compare the two. We have now included the following paragraph in the Discussion: “Finally, we note that although empathy and effectiveness are often discussed in parallel - both in public discourse and in theoretical debates - there are currently too few studies that measure both constructs within the same design to allow formal statistical comparisons between them. This limits the extent to which we can directly evaluate their relative contributions to charitable giving. We therefore encourage future research to explicitly examine both constructs within the same studies, using consistent measures and parallel designs, to allow more direct comparisons of their predictive value.” More of a minor comment: I appreciated the “Reference Category” column in tables 3 and 4. I would also suggest the authors clarify what these reference categories are early in the Methods section. I think this will improve readability. 2 The reference category information is only relevant to the Multiple Moderator Analyses, which are not introduced until paragraph 6 of the Method. As such, we worry that highlighting this information early in the Method section would potentially lead to confusion (i.e., telling the statistical story backwards). For this reason, we feel that the reference categories are best interpreted in context with the rest of the data reported in Tables 3 and 4, but we are happy to re-visit this if the editor or reviewer feel strongly. Reviewer #3: I think the paper makes a solid contribution, but I might recommend the following two changes, which should make the contribution easier to see: (1) The authors use the term “efficacy” to refer to the superset of studies that include both studies that manipulated efficacy as well as studies that measured self-reported perceptions of efficacy. I think it would help make the contribution a lot clearer if the authors would throughout the paper n treat these as two distinct constructs, and not use the word “efficacy” to refer to both or their superset. This is especially important given that the key result, in my opinion, is that psychologically these two constructs—“self reported perceptions of efficacy” and “actual efficacy”—work quite differently; it is hard to clearly present that result—that two constructs work differently—if the authors themselves are using the same word (“efficacy”) to refer to the two constructs. As Reviewer 3 notes, one of the most striking findings in our paper is that these two operationalisations (measured versus manipulated effectiveness) yield markedly different results, and we agree this is a key contribution of our work. At the same time, we are mindful of the need to maintain clarity and readability throughout the manuscript. We worry that using different labels (e.g., “self-reported perceptions of effectiveness” versus “actual or manipulated effectiveness”) at every mention risks introducing redundancy, reducing fluency, and ultimately detracting from the accessibility of the manuscript. This is especially so given that a similar distinction would need to be made for empathy (i.e., measured self-reported empathy vs. manipulated empathy) to be consistent. As a compromise, we have revised the Introduction (see new paragraphs 3 and 4) to explicitly flag this distinction as a central goal of the paper and to clearly state that we treat the two operationalisations of effectiveness separately in our analyses. This framing ensures that readers understand the conceptual distinction and how we handle it in the results, without the need for repeated qualifications throughout the manuscript. We hope this approach strikes a reasonable balance between conceptual clarity and editorial readability. (2) The paper could really use a discussion of what has already been shown about the roles of efficacy, self-reported perceptions of efficacy, and empathy. The introduction describes a debate on the relative roles of empathy and efficacy, but doesn’t summarize the existing evidence that has already been amassed on this debate. This would be quite helpful, in my opinion. Moreover, since the key result, in my opinion, rest on the distinction between self-reported perceptions of efficacy and actual efficacy, I think it would help if there were a summary of what’s already known about that distinction and, perhaps, what’s been hypothesized on why they might be working differently). If it were me, I would include at least a summary of this literature in the introduction, so that the reader can better appreciate and process what the authors are doing and what they have found, before the reader is forced to delve in. 3 We appreciate the reviewer’s point that readers would benefit from a clearer grounding in existing work in the Introduction. While one of the strengths of a meta-analytic approach is that it functions as a structured synthesis of the literature - often reducing the need for an extended narrative review up front - we agree that some additional context in the Introduction would help readers appreciate what is new and meaningful in our meta-analysis. In making our revisions, however, we were also mindful of the fact that we are right on the word limits imposed by Nature Communications. In particular, we were cautious not to front-load the manuscript with an extended literature review, which might duplicate or pre-empt the contribution of the meta-analysis itself. Finally, we are aware of no literature that has formally predicted (or theorised about) the distinction between perceived and actual effectiveness, which is one reason we think the current paper is making a valuable contribution to the literature. To better foreground the existing evidence in this space, we now:  Highlight the fact that prior meta-analyses of empathy and prosocial behaviour have generally excluded experimental designs.  Draw attention to the limited but high-profile experimental studies on effectiveness, and the lack of synthesis to date across correlational and experimental work.  Explicitly cite three high-profile experiments showing that information on effectiveness has limited effect on the behaviours of potential donors. Reviewer #4: The authors thoroughly addressed my previous concerns, and I am happy to sign off on this version. Nice job! We thank Reviewer 4 for the kind words and for their help improving the manuscript in previous rounds. Reviewer #5: The revised version of the manuscript addresses many of the concerns we raised in the first review. However, there remain issues that need to be clarified. 1. Please add the fact that there is significant heterogeneity among studies in their estimates of the correlations in the abstract. The abstract provides the mean correlation and its confidence interval, but does not indicate that there is significant heterogeneity in this estimate as demonstrated in the prediction intervals. Please see Tipton et al. (2023) for a demonstration of the importance of discussing effect size heterogeneity. Tipton, E., Bryan, C., Murray, J., McDaniel, M. A., Schneider, B., & Yeager, D. S. (2023). Why meta-analyses of growth mindset and other interventions should follow best practices for examining heterogeneity: Commentary on Macnamara and Burgoyne (2023) and Burnette et al. (2023). Psychological Bulletin, 149(3–4), 229–241. https://doi.org/10.1037/bul0000384 We have now added reference to heterogeneity in the Abstract, highlighting the importance of testing for moderators. 4 2. While the univariate analyses are interesting, they are subject to potential confounding. This is clear in the meta-regression analysis including all moderators. The self-reported and behavioral measures difference is no longer significant when including all moderators. Thus, the meta-regression results should be the analysis that is interpreted more extensively than the individual univariate analyses. The current manuscript highlights the univariate analyses, and provides a narrative description only of the meta-regression. Since meta-regression and meta-analyses suffer from potential overlapping and confounding moderators, the meta-regression results allow the interpretation of the association among the moderators and the correlations controlling for other moderators. The meta-regression can be estimated in a way to obtain the adjusted subgroup means by deleting the intercept term and thus, the discussion about subgroup differences could use the adjusted means rather than the means from univariate meta-regressions. Table 4 should be the main analysis here. Please see Tipton et al. (2019) for a discussion of meta-regression. Tipton, E., Pustejovsky, J. E., & Ahmadi, H. (2019). Current practices in meta-regression in psychology, education, and medicine. Research Synthesis Methods, 10(2), 180–194. https://doi.org/10.1002/jrsm.1339 Thank you for your thoughtful comments regarding the interpretation of our univariate and multivariate meta-regression analyses. We agree that multivariate meta-regression provides important insights by accounting for potential confounding among moderators. To help clarify why some moderator effects observed in the univariate models did not persist in the multivariate model, we have added a paragraph to the Results section explaining that the no-longer-significant effects (i.e., the moderating roles of self-report vs. behavioural measures, and likelihood vs. value) were likely suppressed due to their shared variance with the measured vs. manipulated distinction. Experimental studies were more likely to use behavioural and value-based outcomes, making it difficult with the current data to completely disentangle their independent effects. Nevertheless, we would like to clarify and justify our analytic strategy, which follows a staged approach to moderator analysis. Specifically, we first conduct univariate meta-regressions to identify potentially influential moderators and then estimate a multivariate model using only those that showed meaningful effects. This approach is well-established in the meta-analytic literature (e.g., Borenstein et al., 2009; Lipsey & Wilson, 2001) and was particularly appropriate given the structure of our data. For example, not all studies included information on every moderator, and our goal was to retain as many studies as possible in each analysis. Conducting a full multivariate model from the outset would have required listwise deletion, significantly reducing the sample size and, in turn, statistical power. Power would also be further reduced by including too many predictors in the model simultaneously. By using univariate models, we were able to include the full set of studies available for each moderator, reducing the potential for bias that can arise when missing data are not random, and thereby provide a more accurate and inclusive picture of the evidence. Indeed, while Tipton et al. (2019) advocate for careful interpretation of meta-regression results, they also recognise that staged approaches - beginning with univariate moderator analyses as we have done - are a common strategy, particularly when moderator data are not fully reported across studies or when model complexity may exceed available power. 5 We thank the reviewer also for raising the possibility of presenting adjusted subgroup means from the multivariate meta-regression model by removing the intercept term. We agree this is a useful strategy in some contexts and appreciate the methodological clarity it can offer. Given the number of moderators in our models and the limited number of effect sizes available for some cells, estimating adjusted means for every subgroup in this way would have introduced instability and reduced interpretability in our already complex models. Instead, we chose to report the coefficient-based contrasts (relative to reference categories) from the multivariate model, and present univariate subgroup means to aid interpretation of the raw patterns in the data. We believe this approach offers a reasonable balance of rigour and accessibility, but we are happy to revisit this decision if the editor or reviewers feel strongly. Borenstein, M., Hedges, L. V., Higgins, J. P. T., & Rothstein, H. R. (2009). Introduction to meta-analysis. Wiley. Lipsey, M. W., & Wilson, D. B. (2001). Practical meta-analysis. Sage Publications. 3. On page 11, line 265, this statement appears, referring to the average correlation in the meta-analysis: “This association was robust, emerging across diverse samples and operationalisations of charitable giving.” This statement is misleading as there is significant heterogeneity across the studies, with a prediction interval ranging from -0.14 to 0.57. The lack of statistical significance for the association among moderators and the correlation does not negate the fact that the studies are reporting a wide range of associations from negative to positive. We have revised the sentence in question to better capture the robustness of the overall effect while clearly signalling the variability in effect sizes across studies. It now reads: “This association was statistically robust across a wide range of samples and operationalisations of charitable giving, although significant heterogeneity was observed.” 4. On page 20, line 472, the manuscript describes the multilevel model used for the analysis. The authors might consider highlighting the assumption in the multilevel model that the effect sizes within studies are considered independent. The multilevel model is one potential model used for dependent effect sizes; Pustejovsky & Tipton (202 ) discuss other models such as the correlated and hierarchical model (the multilevel model assuming a nonzero correlation among effect sizes nested within studies). Pustejovsky, J. E., & Tipton, E. (2021). Meta-analysis with Robust Variance Estimation: Expanding the Range of Working Models. Prevention Science. https://doi.org/10.1007/s11121-021-01246-3 Thank you for raising this important point regarding the assumptions underlying our multilevel model. To clarify, the three-level meta-analytic model we used (following Assink & Wibbelink, 2016) does not assume independence of effect sizes within studies. Rather, it explicitly models the dependence through a nested random effects structure, with separate variance components at the within-study (Level 2) and between-study (Level 3) levels. In this sense, our model accounts for non-independence among effect sizes by allowing for heterogeneity at both the study and effect levels. We recognise, however, that this approach assumes no residual correlation among effect sizes within studies beyond what is captured by the random effects. As noted in Pustejovsky and 6 Tipton (2021), more flexible models - such as those that specify a residual correlation structure or use robust variance estimation - offer alternatives that can accommodate more complex dependence patterns, especially when many effect sizes are drawn from each study. We have revised the Methods section to make this modelling assumption more explicit and have added reference to Pustejovsky & Tipton (2021) to acknowledge these alternative approaches. Given the relatively small number of effect sizes per study in our dataset (average of 2.24), we judged the three-level model to be appropriate and parsimonious for our purposes. We nevertheless appreciate the importance of adding this additional clarity in our Methods. Therefore, we have added the following in the Method: “Specifically, the total variance is partitioned into three components: sampling variance (Level 1), within-study variance (Level 2), and between-study variance (Level 3), thereby accounting for the non-independence of effect sizes within studies. We note, however, that the model assumes residuals are uncorrelated within studies beyond the modelled random effects (Pustejovsky & Tipton, 2021).” 5. The manuscript still includes a few causal statements. On pages 3 and 11 (“to what extent”), and page 8 (“impacted”). On page 8, we changed the sentence “Finally, we examined whether the different operationalisations of effectiveness impacted strength of association” to “Finally, we examined whether the different operationalisations of effectiveness corresponded to differences in strength of association”. We appreciate the concern about potential causal inference. We chose the phrasing \"to what extent\" to indicate degree or magnitude of association, not directionality or causality. This phrase is commonly used in both correlational and experimental contexts, and we believe it accurately reflects the descriptive and quantitative nature of our synthesis. .6. Page 8, line 176 includes a typo, “was perceived to be had no reliable effect”. The original sentence was “In other words, experimental stimuli designed to manipulate how effective a donation or charity was perceived to be had no reliable effect on charitable giving choices”. Although this is not a typo, we agree that the sentence was convoluted and vulnerable to misreading. We have now changed it to “In other words, experimental stimuli intended to influence perceptions of a charity’s effectiveness did not reliably affect charitable giving decisions on average.” 1 RESPONSE TO REVIEWER COMMENTS Reviewer #1: I thank the authors for their revisions. My concerns have been satisfactorily addressed. We thank Reviewer 1 for their contributions to the paper. Reviewer #5: Thank you for this careful revision. My prior comments are now addressed. I have one additional clarification regarding the results of the univariate moderator analyses. In Table 2, each section of the table reports on a single subgroup analysis, comparing the mean effect size from, for example, studies measuring state versus trait empathy. The text on page 10 notes that \"a stronger association was found when empathy was operationalised situationally (i.e., as a state variable; r=.27, p<.001) than when it was measured dispositionally (i.e., as a trait variable; r=.20, p<.001)\". How was this test conducted to make the claim that the correlation of r=0.27 is stronger than r=0.20? Was there a statistical test conducted to examine these differences in an ANOVA-like framework or using a Wald test with contrasts in meta-regression? Many of the univariate subgroup means have overlapping 95% confidence intervals so it is difficult to see how conclusions were drawn from these analyses. For all categorical moderators (including the state vs trait empathy example), we did not infer subgroup differences from visual inspection of the confidence intervals. In these models, the moderator was included as a dummy-coded predictor, and the F-statistic reported in Tables 1 and 2 is a Wald-type omnibus test of the moderator (i.e., an ANOVA-like test of whether the average effect differs across categories). In the specific example the reviewer highlights, the difference between state empathy (r = .27) and trait empathy (r = .20) comes from such a model, and the omnibus test was significant, F(1,254) = 7.06, p = .008. Our statement that the association is “stronger” for state than trait empathy is therefore based on this omnibus test of the difference between subgroup effects, not on overlapping 95% CIs around the subgroup means. As the reviewer notes, overlapping CIs for the two subgroup means can occur even when the CI for their difference excludes zero, which is what the omnibus test captures."}]

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