Meta-analysis

Loading the data

Paste columns directly from the sheet (including the header row) – select them in Excel, copy, and paste here:

Variables and settings

When to use?

When there are several studies that examined the same question – the same intervention versus control, the same relationship between two variables – and the goal is to know what they say together: what the mean effect is, how precise it is, and whether it is consistent across studies. A meta-analysis does this with a weighted average of the effect sizes, in which a more precise study receives more weight. The familiar alternative – counting how many studies came out significant – is wrong: "vote counting" treats a nonsignificant result as evidence of the absence of an effect, although it may stem from low power, and Hedges and Olkin showed that its power may even tend toward zero as the number of studies grows (as cited in Borenstein et al., 2009, pp. 251-252). In the example there, five studies, none of which is significant (p = .265), add up to a significant effect (p = .013).

The computation is the small part. Before getting to it there is a defined question, a systematic search, inclusion criteria and coding – Harrer and colleagues (2021, pp. 9-11) list the pitfalls: "apples and oranges" (studies too different to pool), "garbage in, garbage out" (biased studies), "the file drawer" (unpublished studies), and the researcher's agenda – the last of which can be reduced by preregistering the analysis plan. A meta-analysis of the sensitivity and specificity of diagnostic tests requires bivariate models, which pool both together (Macaskill et al., 2023, p. 203) – the page does not run them; for a single test – the ROC analysis page.

Effect size

Means in two groups. When all the studies used the same scale, the raw mean difference can be pooled, which is understood in the original units; when they used different instruments – only a standardized difference, the mean difference divided by the pooled standard deviation (Borenstein et al., 2009, p. 25). d "has a slight bias" in small samples, so it is corrected to Hedges' g (ibid., p. 27). The variance of g has several formulas, and Borenstein and colleagues themselves note that "slightly different expressions" have been given by different authors (p. 28) – "both-and": the page computes as escalc in metafor does (exact correction, and a variance with g²), and the book uses an approximate correction and the variance of d multiplied by J². The difference is negligible except in tiny samples; in the book's full example the pooled effect is 0.3585 versus 0.3582. The direction is arbitrary, but must be consistent: if positive means the experimental group is better, this must apply to all the studies (ibid., p. 25).

2×2 tables. The risk ratio and the odds ratio are relative measures, "relatively insensitive to differences in baseline rate"; the risk difference is absolute – sensitive to the baseline rate, but sometimes "more clinically meaningful" (Borenstein et al., 2009, p. 38). The ratios are analyzed on the log scale and converted back for presentation (p. 39). When a study has a zero cell, the page adds one half to all four cells of that study, as escalc does.

Correlations. The variance of r depends on r itself, so pooling is done after Fisher's z transformation, and the result is converted back to r for presentation (Borenstein et al., 2009, pp. 41-43).

Partial correlation from a regression coefficient. In policy, public administration and social science research most findings come as regression coefficients, and Ringquist (2013, pp. 104-105) recommends using them in effect sizes from the r family: from the t of the coefficient compute r = t/√(t² + df) – the partial correlation between the predictor and the dependent variable, regardless of the number of predictors in the model; the small bias created by the number of predictors is "negligible" in most cases (pp. 105-106). The sign is that of the coefficient, and it must be made sure that it is oriented consistently across all studies (pp. 137-138). A study that reported only asterisks – plug in the threshold value of t, and the resulting correlation is a lower bound; a study that wrote only "not significant" – it is better to plug in r = 0 than to omit it, because omission "will almost certainly inflate" the mean effect (p. 108). "Both-and" in the variance: Ringquist uses the ordinary variance of Fisher's z, 1/(n − 3) (p. 109); the page computes as escalc("ZPCOR") in metafor does, 1/(n − m − 2) with m predictors – the difference is small in large samples.

Precomputed effect. When studies reported only an effect and a confidence interval, the standard error is the width of the interval divided by 2 × 1.96; for a ratio (OR, RR, HR) – on the log scale. For a g entered this way – make sure the bias correction has already been applied, because the page cannot know (Harrer et al., 2021, p. 105).

Fixed effect or random effects

The fixed-effect model assumes that all the studies share the same true effect and differ only in sampling error; the random-effects model – that the true effect varies between studies, and the goal is the mean of the distribution of effects (Borenstein et al., 2009, p. 77). A fixed effect is appropriate when the studies are "functionally identical" and the goal is not to generalize beyond them – a "relatively rare" situation; when the studies were done by different researchers and gathered from the literature, random effects are "usually more plausible" (pp. 83-86). Harrer and colleagues (2021, p. 101) add that in the social sciences "it is common to always use" random effects, but "both-and": the model gives more weight to small studies, which are sometimes more biased – and some have argued that a fixed effect is sometimes preferable (ibid.). The field-specific books also prefer random effects: Ringquist (2013, p. 33) – "always", unless there are particularly strong reasons to assume a fixed effect, because fixed-effect conclusions apply only to the studies gathered (pp. 120-121); Cooke (2024, p. 133) – psychological studies are not conducted in the same way by different teams, so a fixed effect is "hard to justify". And "both-and": Kumar (2023, pp. 112-113) writes that he himself prefers a fixed effect as long as the variance is not large, and that it is better to investigate the sources of heterogeneity than to model them. The page shows both; the paragraph reports random effects.

What not to do: start with a fixed effect and switch to random effects if the heterogeneity test is significant – this "should be strongly discouraged", because the choice depends on understanding whether the studies share one effect, and the test is weak (Borenstein et al., 2009, p. 84); the model is chosen "at the planning stage" (Kumar, 2023, p. 36). And another difference: with random effects the confidence interval is always wider, and does not shrink to zero even with huge studies – because the number of studies, not their size, limits the precision of the mean (pp. 80-81). When there are very few studies, the estimate of the between-study variance is not precise, and "each of the options is problematic" (p. 84).

The τ² estimator and Knapp-Hartung

The estimator. The between-study variance, τ², can be estimated in several ways. DerSimonian-Laird is the most common and the default in older software, but "may be biased, especially when the number of studies is small and heterogeneity is high". The guidelines of Harrer and colleagues (2021, pp. 102-103), "both-and": REML for continuous effects as a starting point (and this is the metafor default); Paule-Mandel for binary effects; and DerSimonian-Laird when others should be able to reproduce the result outside R as well. "There are no iron-clad rules", and the differences are usually small – it is worth rerunning with another estimator and seeing whether the interpretation changes. The page offers all three.

Knapp-Hartung. The ordinary confidence interval ignores the uncertainty in the estimate of τ². The Knapp and Hartung correction (full name HKSJ) computes a different standard error and uses the t distribution with k − 1 degrees of freedom; in simulations it "works much better" than the Wald test at the numbers of studies common in practice, and in a check of 689 Cochrane meta-analyses, a quarter of the findings significant by the ordinary method were not significant with it (Stijnen et al., 2021, p. 51). Harrer and colleagues (2021, p. 104) consider it "generally sensible", and note that some have argued that in rare cases of very homogeneous effects it is too lenient. The page shows both intervals side by side.

Heterogeneity and prediction interval

Four measures, each with a role (Borenstein et al., 2009, pp. 119-122; Harrer et al., 2021, pp. 140-150): Q and its p test whether there is any true variance at all – but are sensitive to the number of studies and their size; τ² and τ – the variance and standard deviation of the true effects, in the units of the effect; I² – the part of the observed dispersion that is real and not sampling error, a "signal-to-noise ratio" between 0% and 100%. The thresholds of Higgins and colleagues – 25%, 50%, 75% for low, moderate and high – are "tentative" (Borenstein et al., 2009, p. 119), and I² does not say how dispersed the effects are: an I² close to 100% can come from effects in a narrow range estimated very precisely (ibid.). I² also depends on the precision of the studies – with huge studies it tends toward 100% (Harrer et al., 2021, p. 149). The books also differ on the thresholds: Kumar (2023, p. 42) cites Cochrane's overlapping ranges – 0%-40% low, 30%-60% moderate, 50%-90% substantial, 75%-100% considerable – and warns that I² is biased when there are few studies. And when heterogeneity is especially high, the first thing to check is typing errors in the data (ibid., p. 43).

Confidence intervals for heterogeneity. "The uncertainty around τ² or I² is often very large", so "it would be a mistake" to interpret an estimate of zero as evidence of consistency, unless the interval rules out large values (Borenstein et al., 2009, p. 122). The page computes the intervals by the Q-profile method, like metafor and meta (Harrer et al., 2021, pp. 148-149); Borenstein and colleagues (2009, pp. 122-125) have a simpler formula, and this is another place where software differs.

Prediction interval. The confidence interval says how precise the mean is; the prediction interval – where the true effect in a new study is expected to fall, so "the two measures are not interchangeable" (Borenstein et al., 2009, p. 131). As the number of studies grows, the confidence interval shrinks to zero, and the prediction interval does not – it approaches the true dispersion (pp. 132-133). If it is entirely above zero, the intervention is expected to help in other contexts too; if it includes zero – less certain (Harrer et al., 2021, p. 150). The formula – "both-and": Higgins and colleagues (as cited in Borenstein et al., 2009, p. 130) use t with k − 2 degrees of freedom, and this is what the page reports; Harrer and colleagues (2021, p. 150) – k − 1; and predict in metafor – the normal distribution (shown in the reading box). Cooke (2024, p. 165) – who does not report τ² at all (p. 137) – recommends that "prediction intervals be reported routinely".

Subgroups

Subgroup analysis asks whether the effect differs between types of studies – an individual versus a group program, self-report versus expert rating. Within each group – an ordinary meta-analysis, and then the group estimates are compared with a Q test, as if each group were one large study (Harrer et al., 2021, pp. 184-185). An open question – "both-and" – is whether to estimate a separate τ² in each group or one pooled one: separate, when the dispersion is expected to differ between the groups; pooled, when it is assumed to be similar, and also when a group has five studies or fewer, because then the separate estimate is not precise (Borenstein et al., 2009, pp. 162-163). The page computes both: a Q_between test with separate τ², and a mixed model with pooled τ² (Q_M, and the proportion of explained variance R²; p. 179).

Three warnings (Harrer et al., 2021, pp. 188-190): power is low, and the accepted rule is at least 10 studies; the absence of a significant difference is not proof that the groups are equal; and the analysis is "observational only" – even when all the studies are controlled experiments, the groups may differ on other variables (see also Borenstein et al., 2009, p. 209). And another pitfall: splitting by an aggregate variable, such as the mean age of the participants, exposes the analysis to "ecological bias" – an association between studies is not an association between people (Harrer et al., 2021, p. 189). Cooke (2024, p. 146) recommends at least five studies in each group; Kumar (2023, p. 57) cites the clinical convention in which a p smaller than .10 in the test of the difference between the groups already counts as significant, because the test is weak. And Ringquist (2013, p. 142) prefers meta-regression – one model with the group variable as a predictor – over separate meta-analyses for each group, which are "less powerful"; this is exactly the second way on the page (pooled τ²).

Publication bias

Studies with large, significant effects are published more often, so a meta-analysis that relies on the published literature may overestimate (Borenstein et al., 2009, p. 277). The funnel plot shows each study by its effect and standard error; without bias the points scatter symmetrically around the mean, and small studies missing on one side are a warning sign. Egger's test tests the asymmetry by regression (Harrer et al., 2021, pp. 236-238), and trim-and-fill imputes "missing" studies until the funnel is symmetric and computes a corrected estimate (Borenstein et al., 2009, p. 286).

But – and this is the main point – both methods detect a "small-study effect", not publication bias: the effect may be larger in small studies for real reasons (a different population, different rigor, different quality), or by chance (Borenstein et al., 2009, p. 291; Harrer et al., 2021, pp. 235-236). So the wording is "if the asymmetry is due to bias, the analysis suggests that…". The tests are weak, and it is recommended to run them only when there are at least 10 studies (Sterne et al., 2011, as cited in Harrer et al., 2021, p. 242), so the absence of significant asymmetry does not guarantee symmetry (Borenstein et al., 2009, p. 291). Trim-and-fill "does not produce reliable results when heterogeneity is large", and often does not correct enough (Harrer et al., 2021, pp. 243, 282); and no method performs well when I² is around 75% (ibid., p. 282). Newer methods – PET-PEESE, p-curve, selection models – are not on the page, and "there is no clear winner yet" (ibid., p. 281). The best way: a search for unpublished studies (ibid.).

"Both-and" regarding trim-and-fill: Borenstein and colleagues (2009, p. 286) present it as a way to estimate a corrected effect, and Ringquist (2013, p. 256) does not recommend it at all in policy and administration research – when there is real variance between the effects it greatly underestimates the mean effect. Egger's test also becomes too lenient when heterogeneity is large, and its false-positive rate may approach 100% in large, heterogeneous meta-analyses (Peters et al., 2006, as cited in Ringquist, 2013, p. 249). The recommendation there: an exhaustive search including government reports and the gray literature, and a "published / unpublished" variable as a subgroup (pp. 265-266).

Psychology, clinical research, policy

Psychology. Cooke (2024) writes for psychologists, and proposes two effect sizes: r from survey studies and d (on the page – g) from experiments and interventions (pp. 1, 75). Two practical warnings: r = .5 is a large correlation, but d = .5 is a medium effect – and most d values in psychology range between −0.50 and +0.50, so if most of your values are large – "it is worth checking your calculations" (pp. 26, 29); and heterogeneity is the rule, not the exception (p. 135). When a study reported several measures or several time points, one way is to choose or average in advance, and multilevel methods allow including all of them (pp. 167-169) – which the page does not run. Preregistration in PROSPERO and reporting according to PRISMA (pp. 46-47).

Clinical research. Kumar (2023) writes for clinical researchers: a meta-analysis of controlled trials is at the top of the evidence hierarchy (pp. 1-2), and reporting follows PRISMA (pp. 1, 3). For a binary outcome – a risk ratio or odds ratio for pooling, because they are more stable across different baseline rates, and a risk difference to show the clinical benefit (p. 29); for a continuous outcome – a mean difference when all the studies measured on the same scale, and a standardized difference only when they did not (pp. 27-28). The errors he encounters most often: typing errors and swapped numbers, a standard error of the mean entered instead of a standard deviation, and the same study twice (pp. 108-109). In his view at least 10 studies are needed for a valid conclusion (p. 109) – a stricter requirement than is customary, which Borenstein and colleagues (2009, p. 84) put differently: with few studies all the options are problematic.

Policy and public administration. Ringquist (2013) writes for research in which most studies are observational, the effects come from regressions (partial correlation – see "Effect size"), and heterogeneity is the rule (pp. 18, 33). Counting significant studies is especially misleading there: twenty studies with a power of .50 split half and half, and the conclusion that "the evidence is mixed" – is "wrong" (p. 24). So in his view meta-regression is "the main focus" (p. 20); a study usually yields several effects, and the dependence between them must be corrected for (pp. 150-151) – two operations the page does not perform. What the page does provide: subgroups by a study variable (sector, program type, published / unpublished) in a pooled model, like a meta-regression with a single categorical predictor.

How to read the output?

Table 1 – the studies: for each study – the effect size, the confidence interval, the standard error and the weight in both models. Figure 1 – forest plot: the same studies in a graph, with a diamond for each pooled effect and a line for the prediction interval. Table 2 – the pooled effect: fixed effect, random effects, and random effects with Knapp-Hartung. Table 3 – heterogeneity: Q, τ², τ, I² and H² with confidence intervals, and the prediction interval.

When a subgroup is selected – a subgroups table with the estimate in each group in both ways and the tests of the difference in the note. From three studies up – a funnel plot and a small-study effects table (Egger, trim-and-fill), and on a click – leaving out each study in turn: if leaving out one study changes the picture, it is especially influential (Harrer et al., 2021, p. 156).

Assumptions and warnings

One effect from one study. The whole computation assumes that each row is an independent sample. A study that reported several outcomes on the same participants (several scales, several measurement times) is not several studies – entering all of them "will lead to incorrect estimates of the variance" (Borenstein et al., 2009, p. 215); choose one outcome by a rule set in advance, or use methods for complex structures (ibid., part 5), which are not on the page. Independent subgroups within a study (e.g. children and adults) can be entered as two rows (ibid.).

Normal approximation. The analysis treats the standard errors as known and the effects as normally distributed – an approximation that is better in large samples and on the appropriate scales (log for ratios, Fisher's z for correlations); for tiny studies or rare events exact methods are preferable (Stijnen et al., 2021, p. 43), which are not on the page.

What the page does not compute. Meta-regression with a continuous predictor, multilevel and multivariate models, network meta-analysis, the Mantel-Haenszel and Peto methods for 2×2 tables, Peters' test, PET-PEESE, p-curve and selection models, and meta-analysis of diagnostic tests. Limits: at least 2 studies (3 for the prediction interval and the small-study tests); studies with a missing cell in the selected columns – are not included, and the page reports this.

And how do you do it in SPSS?

Recent versions of SPSS Statistics have a meta-analysis menu (Analyze › Meta Analysis), by data type – this is general information about the software, not checked here. PSPP, the free alternative, does not include meta-analysis. So instead of SPSS syntax the page exports an R script with the data embedded in it, which reproduces the output with the metafor package – and it was run in R on the sample data file.

And how do you do it in R?

The metafor package (Viechtbauer, 2010): escalc computes an effect size and variance for each study, rma runs the model (method – the estimator; test = "knha" – Knapp-Hartung; mods – moderators), confint gives confidence intervals for heterogeneity, and forest, funnel, regtest, trimfill and leave1out – the rest. Harrer and colleagues (2021) teach the same material with the meta package. The page is verified against metafor on all the numbers in the output, and the script below was run as is on the sample data file (the values in the comments).

# Meta-analysis – Professor Stat. This file is saved as UTF-8; every comment line starts with an English word
library(readxl)    # reading Excel
library(metafor)   # meta-analysis (Viechtbauer, 2010)

# Loading: row = study; the sheet "Data"
d <- read_excel("C:/Rdata/DATA_meta_example_eng.xlsx", sheet = "Data")
d <- d[complete.cases(d[, c("mean_mentor", "sd_mentor", "n_mentor", "mean_control", "sd_control", "n_control")]), ]   # 17 out of 18

# Effect size: Hedges' g (mentoring minus control) and its variance
d <- escalc(measure = "SMD", m1i = mean_mentor, sd1i = sd_mentor, n1i = n_mentor,
            m2i = mean_control, sd2i = sd_control, n2i = n_control, data = d)

# Random effects (REML), alongside fixed effect and Knapp-Hartung
re <- rma(yi, vi, data = d, method = "REML", slab = study)
re                                                      # g = 0.48 [0.34, 0.62]; Q(16) = 36.07, p = .003; I² = 51.8%
rma(yi, vi, data = d, method = "FE")                    # fixed effect: g = 0.49 [0.40, 0.58]
rma(yi, vi, data = d, method = "REML", test = "knha")   # Knapp-Hartung: [0.34, 0.62], t(16) = 7.35
confint(re)                                             # τ² = 0.042 [0.005, 0.111]; I² [11.3%, 74.1%]

# Prediction interval following Higgins and colleagues – t with k − 2 degrees of freedom (predict uses the normal distribution)
c(re$b) + c(-1, 1) * qt(.975, re$k - 2) * sqrt(re$tau2 + re$se^2)   # interval: [0.02, 0.94]

# Forest plot and funnel plot
forest(re, addpred = TRUE)
funnel(re)

# Subgroups by format (1 = group, 2 = individual): separate τ², and a Q test between the group estimates
sub <- lapply(split(d, d$format), function(x) rma(yi, vi, data = x, method = "REML"))
sub                                                     # group: g = 0.39 [0.23, 0.55]; individual: g = 0.57 [0.35, 0.80]
rma(sapply(sub, coef), sapply(sub, vcov), method = "FE")   # Q between: Q(1) = 1.67, p = .196
rma(yi, vi, mods = ~ factor(format), data = d, method = "REML", control = list(threshold = 1e-10))   # pooled τ²: QM(1) = 1.54, p = .214; R² = 16.0% (without control: 15.9%, early stopping)

# Small-study effects: Egger's test and trim-and-fill
regtest(rma(yi, vi, data = d, method = "FE"), model = "lm")   # Egger's intercept: t(15) = -0.24, p = .812
trimfill(re)                                            # no studies imputed
leave1out(re)                                           # leaving out each study in turn

Reporting the results

Report the model and the τ² estimator and whether Knapp-Hartung was applied – Harrer and colleagues (2021, p. 104) give a sample wording: "as we anticipated considerable between-study heterogeneity, a random-effects model was used… The REML estimator was used to calculate τ²… and Knapp-Hartung adjustments to calculate the confidence interval". And then: the number of studies and participants; the pooled effect with a confidence interval; Q, τ² and I² with confidence intervals, and the prediction interval (Harrer et al., 2021, p. 150); subgroups and bias tests – as planned in advance. A forest plot is an accepted part of the report. The paragraph the page generates is a starting point.

Common mistakes

Counting significant studies instead of pooling effects (Borenstein et al., 2009, pp. 251-252).

Choosing a model by the heterogeneity test (Borenstein et al., 2009, p. 84; Harrer et al., 2021, p. 145).

Reading I² as a measure of dispersion, or an I² of zero as evidence of consistency (Borenstein et al., 2009, pp. 119, 122) – and forgetting the prediction interval.

Pooling a raw mean difference across studies that used different scales (Borenstein et al., 2009, p. 25), or mixing directions – a study in which a high score is bad with a study in which it is good.

Entering several effects from the same study as if they were separate studies (Borenstein et al., 2009, p. 215).

Concluding that "there is no publication bias" because Egger's test was not significant, or that "there is" because it was (Borenstein et al., 2009, p. 291).

Interpreting subgroups as causal, or a nonsignificant difference as equality (Harrer et al., 2021, pp. 188-190).

Labeling an effect "small" or "large" by Cohen's thresholds without context – "a last resort" (Ellis, 2010, p. 42).

Reporting Fisher's z as if it were r. Cooke's example (2024, pp. 102-105) reports r = 0.546 [0.416, 0.676] – but these are z values: converted back, the correlation is r = .50 [.39, .59], and by the thresholds in the book itself (p. 24) – medium, not large. The page always converts back.

Entering a standard error of the mean instead of a standard deviation (Kumar, 2023, pp. 108-109) – the effect inflates, and heterogeneity rises.

Omitting studies that reported only "not significant" – this inflates the mean effect (Ringquist, 2013, p. 108).

References

American Psychological Association. (2020). Publication manual of the American Psychological Association (7th ed.). https://doi.org/10.1037/0000165-000

Borenstein, M., Hedges, L. V., Higgins, J. P. T., & Rothstein, H. R. (2009). Introduction to meta-analysis. Wiley. https://doi.org/10.1002/9780470743386

Cooke, R. (2024). Meta-analysis for psychologists. Palgrave Macmillan. https://doi.org/10.1007/978-3-031-73773-2

Ellis, P. D. (2010). The essential guide to effect sizes: Statistical power, meta-analysis, and the interpretation of research results. Cambridge University Press. https://doi.org/10.1017/CBO9780511761676

Harrer, M., Cuijpers, P., Furukawa, T. A., & Ebert, D. D. (2021). Doing meta-analysis with R: A hands-on guide. Chapman & Hall/CRC. https://doi.org/10.1201/9781003107347

Kumar, A. (2023). Meta-analysis in clinical research: Principles and procedures. Springer. https://doi.org/10.1007/978-981-99-2370-0

Macaskill, P., Takwoingi, Y., Deeks, J. J., & Gatsonis, C. (2023). Understanding meta-analysis. In J. J. Deeks, P. M. Bossuyt, M. M. Leeflang, & Y. Takwoingi (Eds.), Cochrane handbook for systematic reviews of diagnostic test accuracy (pp. 203-248). Wiley.

Ringquist, E. J. (2013). Meta-analysis for public management and policy (M. R. Anderson, Ed.). Jossey-Bass.

Stijnen, T., White, I. R., & Schmid, C. H. (2021). Analysis of univariate study-level summary data using normal models. In C. H. Schmid, T. Stijnen, & I. R. White (Eds.), Handbook of meta-analysis (pp. 41-64). Chapman & Hall/CRC. https://doi.org/10.1201/9781315119403

Viechtbauer, W. (2010). Conducting meta-analyses in R with the metafor package. Journal of Statistical Software, 36(3), 1-48. https://doi.org/10.18637/jss.v036.i03

Hedges and Olkin (1980), Higgins and colleagues, and Duval and Tweedie (2000) – as cited in Borenstein and colleagues (2009); Sterne and colleagues (2011), Schwarzer and colleagues (2015), Pustejovsky and Rodgers (2019) and van Aert and colleagues (2016) – as cited in Harrer and colleagues (2021). Peters and colleagues (2006) – as cited in Ringquist (2013). By the site rule, the reference list includes only sources read in the original; citations are by the printed page. Of the books in the "Meta-analysis" folder, Cooper and colleagues (2019), Cheung (2015) and Chen and Peace (2021) were not cited on the page – their topics (broad research synthesis, SEM, Stata) are outside its scope. From version 2 – also three field-specific books: Cooke (2024) for psychology, Kumar (2023) for clinical research and Ringquist (2013) for policy and public administration. The computation on the page is verified against R 4.3.3 and the metafor 4.4 package (escalc, rma, confint, predict, regtest, trimfill, leave1out), and against the worked examples in chapters 14 and 17 of Borenstein and colleagues (2009) and the two examples of Cooke (2024, tables 7.3 and 10.1).