ALL-IN meta-analysis: breathing life into living systematic reviews and prospective meta-analyses

Statistics

Not all mRNA vaccines showed such favorable results as the Pfizer/BioNTech vaccine. In a press release CureVac AG (2021) announced that the final analysis of their clinical trial observed 83 events in the vaccinated group and 145 in placebo, so only a 43% VE (our calculations assuming a 50:50 balanced risk set (r = 1 in CureVac AG (2020, p. 124))²). Their protocol is formulated in terms of a confidence interval for the vaccine efficacy (VE): the FDA goal is for it to exclude 30%, adjusted for two interim analyses. That adjusted confidence interval at the final analysis is [25.3%, 57.1% VE] (our calculations; normal approximation interval, based on Z α/2-statistic for the nominal level α/2 = 0.02281 (CureVac AG, 2020, Table 8)). Regrettably, this interval does not exclude 30%. When the chips fell, this trial lost.

Statistical analyses like these are essentially all-or-nothing, just as any other p < α analysis. As soon as all the α is spent—either on a few interims and a final analysis or just on one fixed sample size—we cannot continue the trial and perform subsequent analyses without violating the type-I error rate. This might be a reasonable price to pay in the urgency of a pandemic when multiple vaccines are competing, but it is a very inconvenient property for clinical trials in general. Usually, we do want to reanalyze a clinical trial in combination with other similar trials in a meta-analysis. Yet any p < α procedure is equivalent to setting a rejection region for the test statistic and checking whether the value for the statistic falls within that region. This rejection region is based on a sampling distribution that assumes the number of studies in the meta-analysis, and the number of participants within each study to be fixed in advance. Given such a fixed sample size (but also for any sequential stopping rule that sets a maximum sample size in advance, such as α-spending), there is only one region, and your test statistic is either in it or not. If it is not, you are not allowed to redo the analyses with an increased sample size. This problem is recognized in approaches to control type-I error for living systematic reviews (Simmonds et al., 2017). But also if the meta-analysis is not updated, the α is essentially already spent on the individual trial analyses, since the meta-analysis is an update of the trial analysis that is unscheduled and lacks type-I error control at the same level α. If the individual study analysis would have been conclusive, the meta-analysis might never be performed, and we can recognize that we are dealing with a situation of “meta-optional-stopping”. A different way to see this is by the actual sampling distribution of trials in a meta-analysis: any data-driven decision within the series—whether to accumulate more studies and when to perform the meta-analysis—changes the sampling distribution and invalidates the fixed-sample-size distribution assumed for p < α. Hence hardly any meta-analysis has valid type-I error control, when the accumulation of trials is based on strategic decisions, in other words, those that introduce accumulation bias (Ter Schure & Grünwald, 2019).

ALL-IN meta-analysis is not all-or-nothing and can combine all available studies, whatever the intentions of earlier analyses. In fact, it allows any number of new studies or participants to be included without ever spending all α. In terms of gambling, we can keep betting our virtual investment because we never lose everything. The CureVac AG (2021) results, for example, would have accumulated a betting score of 0.81⁸³ · 1.13¹⁴⁵· €1 = €1.84. In the setting of a pandemic with competing vaccines in large trials, this research was not continued. But in other settings, promising, but inconclusive results appear often in smaller trials that should spur new research. The analysis can preserve the evidence to reinvest in the next trial, such that we can continue to observe evidence and express it by betting on additional observations in a new trial. An ALL-IN meta-analysis can always continue testing the null hypothesis—with type-I error control—and estimating the confidence interval—with coverage guarantees. Importantly, for these tests and intervals the procedures are exactly the same no matter what decisions—so-called stopping rules, or accumulation bias processes (Ter Schure & Grünwald, 2019)—are at play. This is not the case for any other approach to type-I error control in living systematic reviews.

Bottom-up living meta-analysis The lack of restrictions on sample size is a unique feature of ALL-IN meta-analysis that sets it apart from other statistical approaches to living systematic reviews (Simmonds et al., 2017), ‘adaptive’ (Tierney et al., 2021) or ‘real-time’ (Petkova et al., 2020) prospective meta-analysis and ‘metatrials’ (van Haren et al., 2021). The only approach that is similar was the proposal of the law of iterated logarithm in meta-analysis (Hu et al., 2007; Lan et al., 2003) and is based on early work by Robbins and colleagues (Robbins, 1970) that is closely related to the methods proposed here (see e.g. Wang & Ramdas (2025) for a comparison with early work). (Our representation based on betting scores/likelihood ratios/e-values has advantages in the ease of communication and its rapidly improving field of statistical methods). Other approaches actually in use require a maximum sample size or a maximum number of studies to guarantee type-I error control for all updates of the meta-analysis. The crucial difference with ALL-IN is that for those methods to be valid, participating in a prospective meta-analysis requires outside control over a trial’s data collection. Outside control is needed in the case of the ‘Framework for prospective adaptive meta-analysis’ (FAME) (Tierney et al., 2021) where a single sample size is set comprised of data from all ongoing trials, possibly at an interim of some of them, and single-analysis statistics is used. The consequence is that the intervals and p-values reported are only valid if never updated, so the analysis assumes that data collection stops after that point. No new analyses are valid after that maximum sample size, since all alpha is spent and possibly accumulation bias is introduced in a re-analysis (Ter Schure & Grünwald, 2019). Similarly, outside control is needed in the operationalization of group-sequential or alpha-spending methods that need the information size relative to the final analysis (Simmonds et al., 2017), and therefore also need to enforce such maximum sample size for the reported results to be valid. Finally, even in in simulation-calibrated Bayesian approaches (Goldfeld et al., 2021; van Haren et al., 2021) restrictions on interims (often) and maximum sample size (always) are imposed for the simulations to terminate. So the frequentist operating characteristics (type-I error, coverage of intervals) of the analysis are not known if trials wish to continue data collection after that maximum sample size and analyze again, or in other ways deviate from the simulated scenarios. Hence all available methods in living systematic reviews and prospective meta-analysis are by design quite top-down, or even explicitly described as “using preestablished stopping rules for safety, efficacy, futility, and harm” (Petkova et al., 2020).

The fact that ALL-IN does not require such outside control for the analysis to be valid not only simplifies the statistics, it also simplifies collaboration as a bottom-up instead of a top-down process. We will illustrate this further in our worked-out example in Section 3 on Collaboration.

Efficiency

Lack of efficiency has been addressed in clinical research in many ways. Not only in the proposal of living systematic reviews (Elliott et al., 2017), but also in encouragements to present new studies in the context of existing evidence (Young & Horton, 2005), in advice to design new trials based on systematic reviews and meta-analysis (Chalmers & Lau, 1993; Goudie et al., 2010; Lau et al., 1995; Lund et al., 2016; Sutton et al., 2007) and in pleading to prevent the “scandal” of wasteful research into clinical questions that are already answered or not of primary importance (Altman, 1994; Chalmers & Glasziou, 2009; Glasziou & Chalmers, 2018; Glasziou et al., 2020; Ioannidis et al., 2014, “research waste”). These calls have not been completely ignored, since clinical research has seen an increase in efficiency—e.g. in platform trials or prospective meta-analysis whenever collaboration is deemed possible prospectively. Nevertheless, most clinical trial data is synthesized retrospectively, and still deserves all of the above recommendations. ALL-IN meta-analysis enables these data-driven decisions that can make science more efficient; any retrospective meta-analysis can become prospective. New studies can be easily informed by the synthesis of all data so far such that exactly the right number of participants are randomized to answer a research question, no more and no less. Moreover, an ALL-IN meta-analysis can give an account of the evidence at any time and therefore facilitate prioritizing new studies, if more than one line of research needs additional data, but not all can be funded.

Collaboration

Any ALL-IN meta-analysis can easily be turned into a prospective meta-analysis and possibly a live or real-time meta-analysis, since it does not matter how many studies will eventually be combined or which study will contribute most data. Whether it is based on summary statistics (Godolphin et al., 2022; Tierney et al., 2021) or on individual participant data (IPD) (Polanin & Williams, 2016), involvement in the same prospective meta-analysis facilitates discussion between those running trials in the same line of research; especially if the line of research can be concluded early. Collaboration in a prospective meta-analysis (PMA) has many advantages, such as reducing research waste and bias (by specifying inclusion criteria and analysis plans in advance) and harmonizing outcome measures (only possible in a close collaboration with trials). Live or real-time PMA can increase the involvement of all trials in such a collaboration, when trials are motivated by the promise of a possible early conclusion (Seidler et al., 2019; and Thomas et al., 2023).

A prospective meta-analysis benefits from homogeneity. With too much heterogeneity, it can be very disheartening to update a random-effects meta-analysis, since many trials are needed to precisely estimate the between trial variation and shrink the interval (Jackson & Turner, 2017; Kulinskaya & Wood, 2014; Sutton et al., 2007). Close collaboration might prevent unnecessary heterogeneity, if trial investigators are involved in the selection of trials in the meta-analysis; especially if they can advise on the design and conduct of new trials and align inclusion criteria and endpoint definitions. A fixed-effects meta-analysis can conclude the research effort early. Sufficient homogeneity may be possible in close collaboration.

Communication

The language of betting The interpretation of evidence in terms of a betting score might help to communicate the uncertainty in statistical results. As Shafer (2021) puts it: “When statistical tests and conclusions are framed as bets, everyone understands their limitations. Great success in betting against probabilities may be the best evidence we can have that the probabilities are wrong, but everyone understands that such success may be mere luck.” Thinking in terms of bets also helps to understand when statistical analyses can be anytime-valid. If they are of the all-or-nothing kind, but reanalyzed in a meta-analysis, they are gambling while broke. (This intuition can be made mathematically precise; see the description of Neyman-Pearson testing in terms of betting Shafer (2021) and Grünwald et al. (2024a)). Yet if we add new studies to an ALL-IN meta-analysis, we are reinvesting the betting score that we saved from earlier studies, to evaluate whether the strategy in those earlier studies continues to succeed. Just like when reinvesting your profits in a casino from one slot machine into another, the notion of winning stays the same. Our evidence against the hypothesis of a fair casino does not change when we alternate slot machines. It does not change if we use the score so far to decide on alternating them or to decide when to cash out. If the slot machines are fair, any strategy of playing them is not expected to make money, and our notion of type-I error control holds under any dependency on past results (stopping rules or accumulation bias processes). This is the intuition that explains why it is statistically possible for the intensions of the analysis to not change its validity, such that the analysis results can change the intentions. Any meta-analysis can become a living systematic review, possibly prospective and possibly real-time.

Other communication Those uncomfortable with the language of betting can also easily resort to any of three more familiar notions of statistical communication. Firstly, the likelihood ratios/betting scores and their generalizations, so-called e-values (Grünwald et al., 2024a; Ramdas & Wang (2024); Vovk & Wang, 2021), can be interpreted as conservative p-values by taking their inverse. If we denote any betting score or e-value by € (e.g. € = 1.84 for the CureVac trial data), then p < 1/€ is a conservative p-value (e.g. p = 1/1.84 = 0.54 for the CureVac trial data). If we communicate the p-value p = 1/€ anyone can test by comparing p < α but with the addition that this conservative p-value is anytime valid³ and so p < α can never spend all α (it is never an all-or-nothing test). Secondly, the likelihood ratios have their own notion of evidence in the likelihood paradigm (Royall, 1997). Just as well as stating that the Pfizer/BioNTech trial (Polack et al., 2020) multiplied €1 to almost €118 million and the CureVac AG (2021) trial multiplied €1 to €1.84, we can state that their data was almost 118 million times and 1.84 times more likely if we assume the FDA’s goal of 50% VE in comparison to assuming only 30% VE. For Pfizer, that sounds very good, for CureVac, not so much, and so these numbers have an interpretation of their own without imposing any α-level. Thirdly, likelihood ratios can be accepted by the Bayesian paradigm, as Bayes factors, and possibly combined with prior odds. Grünwald et al. 2024a and Grünwald (2021) show that betting scores/e-values and Bayes factors are closely related, although not all Bayes factors are betting scores/e-values. The bottom-line for communication purposes is that the reporting by ALL-IN meta-analysis can be interpreted in many ways—p-values, likelihood ratios, Bayes factors—but regardless of the interpretation provide fully frequentist type-I error control for tests and coverage for anytime-valid confidence intervals.

The remainder of this paper discusses the four categories of advantages in more detail: Statistics in Section 1, Efficiency in Section 2, Collaboration in Section 3 and Communication in Section 4. We use the COVID-19 vaccine trials as running examples, based on the FDA COVID-19 vaccine game described already, but also in terms of the e-value logrank test (Ter Schure et al., 2024). In section Section 3 on Collaboration we discuss an example ALL-IN meta-analysis that used this e-value logrank test to study whether the Bacillus Calmette–Guérin (BCG) vaccine, originally developed to protect against tuberculosis and named after its inventors, could protect against COVID-19 (ter Schure et al., 2022). In the concluding section we will provide some broader context, with an overview of all the methods already developed—e-values, safe tests (Grünwald et al., 2024a) and anytime-valid confidence intervals—methods already available in software—notably safestats R package (Turner et al., 2022)—and future work. R code for all calculations, simulations and plots is available through the software availability statement and Ter Schure, 2025, https://doi.org/10.17605/OSF.IO/U6WTP.

1.1 Under the null: e-values in a single trial

To make the FDA COVID-19 vaccine game fair we imposed a multiplication by 2.4 (or 170/70) if we observe the event in the vaccine group and 1.7 (or 170/100) if we observe it in the placebo group. This multiplication has expectation 1 (or smaller) if we assume the null hypothesis of a vaccine with negligible VE of 30% (or smaller). In case of 30%, we have probability 0.41 (or 70/170) to observe a vaccine event and probability 0.59 (or 100/170) to observe placebo, so in expectation we multiply our investment by 1. For example putting 1/3 on vaccine and 2/3 on placebo: 1/3· 70/170 · 170/70 + 2/3· 100/170 ·170/100 = 1. No matter how we invest in the two outcomes, (e.g. try putting 1/2 on vaccine and 1/2 on placebo, or something different) in expectation under the null we multiply the initial investment by 1. This means that our betting score is an e-value, since by definition an e-value is the outcome of a nonnegative random variable with expectation (at most) 1 under the null hypothesis (Grünwald et al., 2024a; Ramdas & Wang, 2024; Vovk & Wang, 2021).

Our betting score could also be rewritten as a likelihood ratio, so the expectation of the likelihood ratio (ℒ(50% VE | X)/ℒ(30% VE | X)) is 1 as well. We hence-forth write the likelihood ratio after n rounds of betting (or after observing n events) as LR⁽ⁿ⁾, with for the FDA COVID-19 vaccine game

Using its expectation of 1, Markov’s inequality bounds the probability of observing a large multiplication of our investment (a large likelihood ratio) by α after n = 170 rounds as follows:

Figure 1 shows at the right side the histogram of betting scores in the FDA COVID-19 vaccine game after 170 events when we simulate events under the null hypothesis, with probability 0.41 to occur in the vaccine group, corresponding to 30% VE. A line is shown at 40, and indeed no more than α = 1/40 = 2.5% of the scores seem to be larger than that threshold. In fact, in these 1000 runs of simulation only 0.3% of the runs have a betting score larger than 40; Markov’s inequality is a loose bound. We also have a stronger result because we obtained our betting score over events by multiplying the score of the rounds (see (1), corresponding to reinvesting our winnings), called Ville’s inequality. We get the following from Ville (1939):

Figure 1. 1000 simulated betting scores in the FDA COVID-19 vaccine game over betting rounds n assuming a probability of 0.41 (70/170) for each event to occur in the vaccine group (the null hypothesis of 30% VE) and optimal Kelly betting for 50% VE.

The dashed line is the threshold 1/α = 40 one-sided. The histogram at the right shows the betting score/LR⁽¹⁷⁰⁾ after 170 events. Note that the expectation of 1 of the scores is not the mode of its distribution nor its median and that the vertical axis is on a logarithmic scale.

Ville’s inequality is also illustrated in Figure 1: if we take the sequence of rounds into account, still only a few out of the 1000 simulations ever reach a betting score larger than 40. In fact, in these 1000 runs of simulation only 1.1% of the runs have a betting score that is larger at any round in the game, such that our type-I error is controlled at α = 2.5% at any time. Moreover, this type-I error control is not tied to this maximum number of 170 events, but continues to hold with an unlimited horizon. Making a large profit in such a fair game casts doubt on the null hypothesis and is captured by a likelihood ratio that grows away from 1: a large betting profit is obtained if the null likelihood is performing worse than alternative.

When trials can be summarized as bets Before they can be combined in a meta-analysis, individual trials are often characterized by the summary statistics from trial publications. Conventional meta-analysis combines these statistics (e.g. mean differences and standard deviations) in a Z-statistic (Borenstein et al., 2009). Unlike the vaccine/placebo outcomes that we have seen so far, such a Z-statistic has a continuous density and cannot be summarized by separately dealing with all possible outcomes. Fortunately, Shafer (2021) shows that any likelihood ratio of distributions can be viewed as a betting score in a game with initial investment €1. This is possible because likelihood ratios have expectation 1 in general if we assume the null hypothesis in the denominator of the ratio to generate the data. For a Z-statistic we have two normal distributions with variance 1, one with mean µ₀ under the null hypothesis, and one with µ₁ under the alternative. If the data is generated by the null model, the expectation of the likelihood ratio is

since ϕ_µ1 (z) is a probability density that integrates to 1. This means that any such likelihood ratio for a Z-statistic is an e-value and can be used to construct tests by betting.

Not all summary statistics can be assumed to form a Z-statistic with a normal distribution. Fortunately for the logrank statistic this is reasonable (Ter Schure et al., 2024) if studies are large and the effect size not too extreme (hazard ratios not too far away from 1). We will use the logrank Z-statistic as a running example for meta-analysis on summary statistics. For an IPD meta-analysis (on individual participant data), however, we recommend to use the exact e-value logrank test from Ter Schure et al. (2024) that is valid regardless of the randomization (e.g. 1:1 balanced or 1:2 unbalanced), the number of participants at risk, the number of events or the size of the effect.

1.2 Under the null: e-values in a (live) meta-analysis

Assume we want to perform a meta-analysis and we collect a Z-statistic Z_i from each trial i, e.g. a logrank statistic. Before observing Z_i we construct an honest bet LR_i = ϕ_µ1(Z_i)/ϕ_µ0(Z_i) for each trial that is an e-value and thus has type-I error control under the null hypothesis ϕ_µ0—for a default logrank statistic this is always µ₀ = 0 corresponding to hazard ratio of 1. If we think of the betting score from the first study and invest it in the second study, we are in fact multiplying likelihood ratios. We need to have a notion of time t, such that at each time we know the number of studies k〈t〉 so far and the number of observations n_i〈t〉 in each study i. Note that for the logrank statistic, and time-to-event in general, the number of observations or sample size n is the number of events. If we assume that all studies are completed at time t with n₁, n₂, ... , n_k events summarized by logrank Z-statistics $z_1^{(n_1)},z_2^{(n_2)},\dots ,z_k^{(n_k)}$ we can construct our ALL-IN bet as follows:

The global null hypothesis Each trial bet is testing the same null hypothesis µ₀ = 0 in (3), such that the ALL-IN meta-analysis bet tests a global null hypothesis of no effect (0% VE, hazard ratio 1) in all trials. Such a global null hypothesis can be rejected with a contribution from each trial, but also in case only one trial observes a large score betting against the hypothesis and no other trial observes a very small betting score that loses those winnings again. After all, the global null (null in each trial) is rejected as soon as the null is rejected in one of the trials.

Meta-analysis on interim data We can generalize this ALL-IN meta-analysis bet of completed trials to bets on interim data by assuming that we only have an interim logrank Z-statistic z₁〈t〉, z₂〈t〉,..., z_k〈t〉 for the n₁〈t〉, n₂〈t〉,..., n_k〈t〉 events observed so far at time t; k〈t〉 still represents the number of studies so far at time t, but now these studies are not (all) completed. We construct our ALL-IN bet in a similar way:

From the perspective of Ville’s inequality, the analysis on completed trials and the one on interim data are indistinguishable. The only thing that matters is that we include all the data we have so far at time t, such that we have type-I error control

for the global null hypothesis probability P₀ with an unlimited horizon over time t. This is why any ALL-IN meta-analysis can become prospective and live or real-time on INterim data. The reported analysis is the same, no matter the intentions of the analysis.

1.3 Under the alternative: optimality in a single trial

A power analysis sets a very specific goal for a trial, usually to detect an effect of minimal clinical importance (MCID, minimal-clinically important difference) or smallest effect size of interest (SESOI). This is the effect we would not like to miss if it were there, although we hope that the real effect is larger. We nevertheless use this effect size of minimal clinical importance to decide on the sample size of the trial, otherwise we risk a futile trial. The FDA was clear on what this minimal effect should be for the COVID-19 vaccine trials: a VE of 50% (FDA, 2020). This is the effect we used to bet in the FDA COVID-19 vaccine game.

Our strategy in the FDA COVID-19 vaccine game, however, was not trying to achieve optimal power. If we compare the all-or-nothing confidence interval for CureVac AG (2021) from the introduction—the final analysis on 83+145 events—we notice that this confidence interval [25.3%, 57.1% VE] is smaller than the final anytime valid confidence interval we show in Figure 3 in Section 1.5, which is [17.1%, 61.6% VE]⁴. The difference is that the former one is optimized to have spent all α at the final analysis, while the latter one is optimized to continue data collection. Power is the probability of finding the desired result using the specified analysis at a sample size or stopping rule. So for an analysis that is intended to have unlimited horizon, power is not a well-defined concept. Instead the literature on e-values (Grünwald et al., 2024a) optimize the expected rate at which the evidence grows for each new data point, not at a specific sample size (Grünwald et al. (2024a) called growth-rate optimality (GRO) in Grünwald et al. (2024a), log-optimality in Ramdas & Wang (2024), and the unique e-value that is optimal in this way the numeraire (Larsson et al., 2024)). The worst case here is the 50% VE for a one-sided alternative hypothesis H₁ = { P_VE : 50% ≤ VE ≤ 100%}. We optimized the FDA bet in the introduction by putting this 50% VE in the alternative likelihood. This can be rewritten in terms of a likelihood ratio for the logrank statistic Z as follows:

with ${\mu }_{\min }=1\text{/}2\log (0.5)and{\mu }_0=1\text{/}2\log (0.7)$ with 0.5 and 0.7 the hazard ratios corresponding to VE of 50% and 30% respectively (see Ter Schure et al. (2024)). So our one-sided alternative hypothesis for the logrank Z-statistic is a Z-distribution with a mean representing an effect that is at least µ_min ('at least' here means more negative, since for a hazard reduction µ_min is negative):

(since positive VE corresponds to a negative µ). Our choice of the parameter of the alternative likelihood µ_min follows directly from the minimal effect set by the FDA. Kelly (1956) already showed that this way of betting optimizes the way our betting score grows if the true VE is 50% (our worst-case scenario). Breiman (1961) showed that this approach also minimizes the expected number of events we need to reach a given betting score set in advance (e.g. €1/α), for which some intuition is given in Figure 2. Grünwald et al. (2024a), Shafer (2021) and the appendix to Ter Schure et al. (2024) give various other reasons why this is the best way to bet, relating it to data compression, information theory, Neyman-Pearson testing, Gibb’s inequality, and Wald’s identity. The most crucial property for the purposes of ALL-IN meta-analysis is that the alternative likelihood puts some money on each possible outcome, such that no matter what outcome we observe, we keep some of the money we risk: our betting score can become small but not 0. This contrasts the approach with a classic p < α test that essentially puts all money on the rejection region, such that if the outcome is not in it, we lose all and cannot continue betting. A thorough interpretation of Neyman-Pearson testing and p-values in terms of betting is given by both Grünwald et al. (2024a) and Shafer (2021).

Figure 2. N_α is the expected number of events needed to reach a betting score of 1/α = 40 for α = 0.025 if we bet according to VE₁ indicated by the three different lines, with bets each of the form ${\displaystyle {\prod }_{i=1}^N\frac{ℒ({\text{VE}}_{\text{1}}|X_i)}{ℒ(30\%\text{VE}|X_i)}.}$

The number of events we need decreases if the true Vaccine efficacy (VE) underlying the data increases (the true difference in risk between vaccine and control is larger). The smallest number of events for a true VE of 40% is reached by betting VE₁ of 40% (blue solid line), the smallest number of events for a true VE of 50% by betting VE₁ of 50% (orange dotted line) and the smallest number for true VE of 60% by betting VE₁ of 60% (grey dashed line). Note that for the alternative in the FDA COVID-19 vaccine game H₁ = { P_VE : 50% ≤ VE ≤ 100%} we are only interested in playing the game well if the true VE is 50% or larger. Since for larger true VE, taking VE₁ = 50% performs quite well, our strategy is to optimize for the worst case of 50% VE itself and use the bet with VE₁ = 50% in the FDA COVID-19 vaccine game. This figure uses Wald's identity. Specific calculations are available in R code on OSF linked in the Software availability section.

Figure 3. Anytime-valid 95%-confidence intervals for a random ordering of the 83 events in the vaccine group and 145 events in placebo from the CureVac AG (2021) trial.

Note that the vertical axis is on a logarithmic scale and that the hazard ratio scale on the right is flipped: smaller values at the top mean smaller risk in the CureVac vaccinated group and therefore larger vaccine efficacy.

1.4 Under the alternative: optimality in a meta-analysis

ALL-IN meta-analysis allows for a retrospective meta-analysis that is bottom-up. The betting score that we accumulate by reinvesting from one trial into the other (which is multiplying betting scores) has an interpretation without enforcing a common design or stopping rule on all included trials. This is especially important if trials have their own stopping rules, or if accumulation processes are at play that influence the existence of trials based on earlier (trial) results in the same meta-analysis. While a meta-analysis can be bottom-up and each have its own design and effect of minimal interest, it can be advisable to agree on a µ_min for the meta-analysis. However, the meta-analysis betting score can also allow each trial i to have its own alternative likelihood with parameter µ_min(i). Then the following multiplication of those betting scores is still a valid meta score with type-I guarantees:

As long as ${\phi }_{{\mu }_{\min (i)}\sqrt{n_i}}$ is a probability density that integrates to 1, we have that each likelihood ratio integrates to 1 under the global null hypothesis, such that (5) holds. This means that trials can also learn their parameter µ_min(i) from already completed trials. Sometimes trials are not powered to detect an effect of minimal interest, but an effect that is plausibly true based on earlier research. Kulinskaya et al. (2016) shows that such use of existing studies to power new trials can actually bias conventional meta-analysis since it introduces yet another dependency between sample size and results that is unaccounted for in any analysis that assumes a fixed sample size. For ALL-IN meta-analysis this is no problem at all, and trials can learn from each other as long as the parameter µ_min(i) is fixed before seeing new data that is evaluated using that parameter in (7). In Ter Schure et al. (2024) we discuss the advantages of even learning the parameter within one trial using prequential plugins or Bayesian updating. In a game like the FDA COVID-19 vaccine game with a clear goal, this is inferior to GRO/log-optimality, but in other situations it could be preferred.

1.5 Anytime-valid confidence intervals

The CureVac AG (2021) trial reached their final interim analysis but was not able to reject the null hypothesis of 30% VE. The trial had also been optimistically powered for 60% instead of 50% VE (CureVac AG, 2020). If a trial is underpowered but still has a large number of participants in follow-up, there is good reason to continue the trial, or combine the trial with results from a new trial in a meta-analysis. However, with a total of 227 events this trial was not underpowered to reject the null hypothesis with an effect in the same ballpark as the Pfizer/BioNTech trial that reported 95% VE (Polack et al., 2020). In such a case it is very interesting to zoom in on the estimate for the effect, instead of its test.

A standard confidence interval can be seen as an inversion of a hypothesis test: if the null falls outside a two-sided 95%-confidence interval it can be rejected with a one-sided type-I error level of α/2 = 0.025. In general, the interval excludes all the values for the parameter that can be rejected when representing the null hypothesis. Similarly, in our context, an anytime-valid confidence interval excludes all values of the parameter that can be rejected by the e-value test that corresponds to the betting strategy at hand. So the interval is essentially tracking a whole range of bets, each against a different null hypothesis. Figure 3 gives a sequence of anytime-valid 95%-confidence intervals for a random ordering of the CureVac AG (2021) data, one for each new observed event or betting round. It shows that the more events we observe, the more parameter values (values for hazard ratios, or their corresponding VEs) we can exclude from the interval. Because these intervals are valid at any time, once we can exclude a value, we never have to include it again. So we also show a sequence of intervals that is the running intersection of all the previous intervals. This of course crucially depends on the ordering, so the one shown for the CureVac AG (2021) data is just an example, since the ordering is randomly chosen. Since these intervals are anytime valid, it is possible to further shrink the intervals by continuing follow-up and observing more events. The coverage of an anytime-valid confidence interval—like an e-value test—has an unlimited horizon.

An ALL-IN meta-analysis confidence interval that is based on a running intersection is of course only possible in an IPD meta-analysis, and cannot be based on summary statistics. The confidence interval shown in Figure 3 is based on the logrank Z-statistic (by repeatedly calculating it after each event), which can also be a summary statistic to achieve a single interval that is anytime-valid. The interval follows from the likelihood ratio of normal densities from (6) and follows a general recipe for constructing anytime-valid confidence intervals from Howard et al. (2021) where the hazard ratio is obtained by maximum-likelihood. The same approach can be used to obtain an ALL-IN meta-analysis confidence interval by weighing the estimates by inverse-variance (the fixed-effects approach) that Peto (1987) calls a typical hazard ratio. We illustrate this approach in our example ALL-IN meta-analysis in Section 3 on Collaboration (for technical details see the Statistical Appendix of Ter Schure et al., 2022) and discuss it a bit further in the final section on future research.

2.1 The evidence so far and what is still needed

An ALL-IN meta-analysis can set a prospective goal for conclusion, e.g. α = 0.0025 = 0.05² corresponding to the level of α required by authorities like the FDA that ask for two trials at the α = 0.05 level. Following Ville’s inequality (5) we need a betting score of 1/α = €400 if we start with €1 to reach a conclusion. Because an ALL-IN meta-analysis combines trials by reinvesting or multiplying betting scores, a very simple calculation gives the betting score we still need at any given point. If an initial trial is able to reach a score of €8, any new trial can be designed to multiply that by 50. So on its own, starting with €1 instead of €8, it would need a betting score of €50 to help the meta-analysis reach €400. We could evaluate the sample size of the new trial on its ability to reach 50, which for a fixed sample size gives the conditional power of the ALL-IN meta-analysis once the new trial is added. However, if this second trial also foresees recruitment issues, it is more difficult to evaluate its planned contribution since it will probably not be the final trial in the meta-analysis. For this, we propose a continuous notion of the ability of a study: the anticipated e-growth. This concept was first proposed by Shafer (2021) to accompany the betting score or e-value with a study design property that "tells a coherent story" unlike power and p-values where power requires a fixed significance level while the p-value does not. Shafer's concept 'implied target' specifically focused on settings in which the betting strategy is not explicit because no alternative hypothesis is specified. Here we focus on an explicit alternative hypothesis and sample size anticipated in the study design, and propose the term 'anticipated e-growth' to evaluate what a single study is thought to add to an existing line of research. We mostly use this concept to compare the ability of various studies in a meta-analysis to each other, and judge whether new studies can conclude the meta-analysis in terms of the assumptions of their study teams. The concept of 'power' does not have that cumulative nature. In statistical literature, power can also be a confusing concept because it is used both as a property of the study and as a property of a statistical test (for statements like 'the chi-squared test has more power than the Fisher exact test). In the literature on testing by betting and e-values, we do not use the same term for both properties, and use 'anticipated e-value growth' for a property of study design, and use the term 'e-power' (Ramdas & Wang, 2024) for the property of an e-value test.

2.2 The ability of a new trial: the anticipated e-growth

The betting score, e-value or likelihood ratio summarizes the data not in just two categories—statistical significant or not statistical significant—but captures the evidence so far on its way to a certain threshold. Similarly we propose to not evaluate experimental design as all-or-nothing, but summarize its ability to build on what is already there and facilitate future research. To capture a study’s expected contribution to a series of studies, we formulate the anticipated e-growth as the multiplicative amount with which the combined evidence is expected to grow if the study—designed with a certain µ_antic and sample size n—is added. In general, the anticipated e-growth E ^* is defined on a Z-statistic as follows:

The logarithm appears in equation (8) because the distribution of a betting score/e-value/likelihood ratio based on n events is very non-symmetric and heavy tailed, with extremely large likelihood ratios occurring with not so small probability (see Figure 4). So the expectation of the likelihood ratio is drawn very far from its typical values by these large likelihood ratios and is not a good expression of what to expect. The logarithm makes the distribution more symmetric (asymptotically (for large n) and for normal likelihood ratios even normally distributed), such that the expectation is a more meaningful summary of the evidence promised by the study. By exponentiation (exp()) we bring this expectation back to the scale of the likelihood ratio, such that it can be interpreted as a betting score or e-value.

Figure 4. (and Figure 5) 1000 simulated sequences of betting scores by round in the FDA COVID-19 vaccine game after 160 events assuming a probability of 0.29 (40/140) for each event to occur in the vaccine group.

This is the alternative hypothesis of 60% vaccine efficacy (VE) used to power the CureVac AG (2020) trial at a number of events of 160. The dashed line is the threshold 1 /α = 40 one-sided and the solid line is the anticipated e-growth of €104. Note that the horizontal axis is on a logarithmic scale.

In the FDA COVID-19 vaccine game the expected growth rate per new event in the CureVac trial, assuming their effect of minimal interest of 60% VE, is the following:

The cumulative contribution of each new event is shown as the linear line on a logarithmic scale in Figure 5. The CureVac AG (2020, Table 8) design planned a final analysis at n = 160 events, so their anticipated e-growth was 1.029454 ¹⁶⁰ ≈ 104. In comparison to anticipated e-growth of €104 at 160 events, the actual betting score €1.84 after 83 + 145 = 228 events in the press release is quite disappointing.

Figure 5. (See above at Figure 4).

The histogram for the final betting scores at the right shows the larger scores above and the smaller ones at the bottom, which means that if we turn it, it is the mirror image of the histogram in Figure 4. The dashed line is the threshold 1 /α = 40 one-sided. The increase in the solid line per additional event/betting round shows the contribution to the anticipated e-growth of each event, up until the anticipated e-growth at n = 160 of 104. In this figure, the design has an approximate 79% power to observe a betting score/e-value larger than 1 /α = 40 before 160 events and 72% power at exactly 160 events (better visible in Figure 4). Note that the vertical axis is on a logartihmic scale.

2.3 Honest study design

An anticipated e-growth does require an honest proposal of the anticipated effect µ_antic, to evaluate the merits of the study. In reality, sometimes this parameter is tweaked—e.g. setting an unrealistically large effect—to still argue for the study’s advancement with only small sample size. Or the effect size of minimal clinical importance is set after data is observed (Wang et al., 2018). This behavior is incentivized by the all-or-nothing character of Neyman-Pearson tests that also make the power analysis all-or-nothing. If your desired sample size does not meet the power hoped-for, you need to either increase it or abandon the study. This aspect of traditional analyses fully ignores the ideal of cumulative science in which one study is not expected to single-handedly answer a research question and small increments in knowledge are valuable, as long as they build towards a common goal. If they use e-values and the ALL-IN framework, researchers do not have to view their analysis as the final one, which helps them to design their study more honestly (Lakens, 2022).

3.1 Outside control not necessary but keeping track of results in a dashboard

Trial researchers might hesitate to collaborate if that means outsourcing decisions in their trial on early stopping or extending follow-up to an outside committee, such as a meta-analysis Data and Safety Monitoring Board recommended by others for ‘real-time’ meta-analysis (Petkova et al., 2020). Instead, the ALL-IN approach allows for a ‘soft’ threshold that merely guides the trials; the leading source of information, but not enforcing anything. This threshold can set a stopping rule, but not in the strict sense that any rule would for a group-sequential or simulation-calibrated design. Those are much stricter because the analysis becomes invalid when the stopping rule is not enforced. In the ALL-IN approach, the threshold can inform how close to a conclusion the meta-analysis is, while also allowing individual trials to continue their follow-up based on trial-specific rationalizations. Adding new events (or even trials) after the threshold is crossed does in fact not invalidate the interpretation of the analysis.

In the ALL-IN-META-BCG-CORONA collaboration, the interim meta-analysis results were communicated through a dashboard. Access to the dashboard could be managed by adding logins and changing permissions to inspect data, and was first only given to one person per trial that was necessarily already unblinded to their own trial results: the one uploading the data for the meta-analysis. At first, each data-uploader received a dashboard account with permissions only to inspect the meta-analysis e-value and their own trial contribution. This access of interim meta-analysis results in the dashboard served as a motivator to keep their own trial data upload up-to-date and to check the sequence of e-values for errors. After an initial period where the data-uploaders could only inspect their own trial results, they granted each other permission to inspect all the individual trial contributions. When the first trials were completed and the meta-analysis was approaching its conclusion, the results were also presented to the Advisory and Steering committees. Figure 6 shows this dashboard based on a demo login with synthetic data (this demo was available for everyone involved from the start to get an impression).

Figure 6. Dashboard used to communicate interim results in ALL-IN-META-BCG-CORONA to all data uploaders with a login.

The trials were performed in the Netherlands (NL), Denmark (DK), the United States (US), Hungary (HU), Brazil (BR), France (FR) and Guinea-Bissau/Mozambique (AF)⁶. The dashboard is in demo mode and shows synthetic (“fake”) data. The option to (de)select trials is for plotting purposes of individual trial e-values; all trials in the dashboard stay included in the meta e-value, following the decision from the Steering committee on trial inclusion. Note that the vertical axis is on a logarithmic scale.

A dashboard for ALL-IN meta-analysis allows to spot trends in the accumulating evidence, and allows any stakeholder to monitor the evidence to prepare for crossing a threshold in the near future, e.g. for independent data monitoring committees of ongoing trials or for those considering new trials or preparing to update medical guidelines. On a log-scale, the increase in e-values is linear (in expectation, see Figure 5) and the observed trends can be projected forward in time, e.g. in Figure 6 as an increase in evidence per additional calendar day.

For ALL-IN-META-BCG-CORONA, the time unit t in the definition of LR^〈t〉 from (4) was set to calendar days and the e-values were updated at each calendar day with an event. The dashboard plots in Figure 6 horizontal lines at 1 for trials that do not observe any events yet: they have not started betting and are still at their initial investment of €1 contributing a neutral amount to the multiplication meta- e-value. ALL-IN meta-analysis monitors e-values as events come in, also when they do so from multiple trials simultaneously. In the language of betting, even the analysis of simultaneous events is considered a sequential bet. If the bet on the events from one trial pays out €4, it multiplies our initial capital by 4, and if the events from another trial pay out €5, it does so by a factor 5. Yet if we actually consider those trials to be consecutive bets, we reinvest the €4 from the first into the second, and obtain €1 · 4 · 5 = €20, as follows from the definition of the meta-analysis e-value on interim data in (4).

A dashboard such as in Figure 6 encourages inspection of each individual trial’s contribution to the meta-analysis. Since each trial’s contribution is a simple multiplication, their components can often be conveniently spotted in the agreement of the shape of the meta-analysis and individual trial lines in a dashboard like Figure 6 (as long as not too many trials are contributing simultaneously).

3.2 Top down or bottom up: the design of the trials and the meta-analysis design

The design of the meta-analysis was mostly top-down by a Steering Committee, but could have also included per-trial elements. In the ALL-IN-META-BCG-CORONA project it was possible, and deemed preferable, to let the Steering Committee decide on an IPD meta-analysis on interim data (‘real-time’) and write protocols and statistical analysis plans, still fully blinded to any results. This timestamped three important decisions on the meta-analysis design: the null hazard ratio of 1 (VE₀ = 0%), the hazard ratio of minimal interest of 0.8 (VE₁ = 20%) and the level of α set at 0.0025 so the threshold for the e-value was at 1/α = 400. Of these, the hazard ratio of minimal interest could have also been set differently for each trial based on individual trial designs, but not all of the trials in the collaboration were powered to detect an effect-size of minimal clinical importance specified on COVID-19 infections. So this effect-size set in a top-down manner, preregistered (Van Werkhoven et al., 2021) and communicated through a webinar and newsletter and discussed in meetings, where each trial was represented by two member in the Advisory Committee. All documentation was made available on a project website (Ter Schure et al., 2020a), and later added to a replication package (ter Schure, 2022a) that now accompanies the (ter Schure et al., 2022) publication.

Anticipated e-growth Table 1 shows that most trials were powered for a different outcome measure⁷ (indicated with ‘*’ in the VE column) and that large effect-sizes were anticipated that were informed by observational studies. The SA trial publication, for example, reports powering ‘to detect a clinically relevant target difference of 75% shown in prior BCG studies’ (Upton et al., 2022). Table 1 shows a simulated anticipated e-growth under this VE in a simulation that decreases the number of participants at risk after each observed event and calculates the exact e-value (see Ter Schure et al. (2024)). The approximation based on a stable risk set introduced for the CureVac data in Section 2.2, gives a close estimate in case the number of events is small compared to the number of participants at risk, e.g. for the US trial:

The anticipated e-growth in Table 1 show that these three trials alone were anticipated to reach the 400 threshold (173.5 · 43.2 · 3.3 >> 400) and that while the SA and US trial were expected to be more important, the BR trial would still contribute, even if small on its own. As with any study design, assuming a larger effect size (larger true VE in the power analysis) results in more convincing test statistics—and the e-value is a test statistic as well. But while too optimistic effect sizes result in ‘nothing’ in an all-or-nothing analysis—results with wide confidence intervals and large p-values—a promising but inconclusive e-value can still contribute to the line of research when combined with new data to continue reaching a conclusion.

The US, HU, BR and AF trial in this ALL-IN-META-BCG-CORONA example did not manage to recruit their intended number of participants and observe the number of events. ALL-IN meta-analysis is ideally suited to still combine such data into a meta-analysis, since the analysis method does not rely on prespecified alpha spending and therefore requires no rule on the number of events. After all, the procedure of analyzing interim data is exactly the same as for analyzing a trial that is completed.

E-values The e-values show that the trials collect little evidence against the global null hypothesis. Table 1 shows exact e-values following the methods based on Individual Participant Data proposed by Ter Schure et al. (2024). These e-values in Table 1 can also be recalculated based summary statistics, specifically the logrank Z statistic and number of events as the Gaussian e-value (see equation (6) in Section 1.3), as reported in Table 1. Gaussian e-values are likelihood ratios of Gaussians comparing the HR of minimal clinical relevance to the null based on the logrank Z statistic. For example, the e-value for COVID-19 infections in trial NL can be recalculated as

Figure 7 shows that also in retrospect the e-values were never close to the threshold of 400. Interpreted as a likelihood ratio, e-values below 1 mean that the likelihood of the null (VE of 0%) is better than the likelihood of the effect-size prespecified as minimal importance (VE of 20%).

Figure 7. Exact logrank e-values over time from the Secondary analysis of ALL-IN-META-BCG-CORONA with the final e-values also shown in Table 1.

Note that the vertical axis is on a logarithmic scale.

Anytime-valid confidence intervals The lack of support for 20% VE as the effect-size of minimal clinical relevance raises the question how well the null of 0% VE is supported compared to other small effects, which is answered by the confidence intervals shown in the forest plot of Figure 8 and running forest plot in Figure 9. These anytime-valid intervals depict all values of the hazard ratio/VE for which, if taken as the null hypothesis in an e-value, the e-value is not reaching the threshold at the 5% level, i.e. e < 1/0.05 = 20 (here we use a more lenient treshold than the 400 used in Figure 7 to reject the null early). So excluded from the interval are all values that are discredited because a successful bet was possible, resulting in a large betting score or e-value > 1/0.05 = 20.

Figure 8. Forest plot for the final Secondary analysis of ALL-IN-META-BCG-CORONA.

The figure shows intervals for the fixed-effects estimate advocated by Richard Peto (1987) as the ‘typical effect’. The anytime-valid confidence interval for the HU trial is (<0.01, >99). Note that the horizontal axis is on a logarithmic scale. The hazard ratios for the trials are estimated by maximum likelihood but can also be approximated based on the excess events and total events (n) reported in Table 1 using the Peto method (Yusuf et al., 1985, pp. 366-367, Statistical Appendix, see also Simmonds et al., 2011) and the approximate sum of variances of the sum(O-E) assuming a stable risk set, of n·(½)·(1 – ½), e.g. for the complete ALL-IN meta-analysis: exp (sum(O−E)/sum(V) ) = exp (-2.0/ (575/4)) = 0.986.

Figure 9. Simplified sequence of forest plots for the Secondary analysis of ALL-IN-META-BCG-CORONA including only three out of seven trials for a less busy plot.

These make up 80% of the total meta-analysis weight (ter Schure et al., 2022) (see all seven and their weights in the final forest plot in Figure 8). The figure shows ALL-IN meta-analysis intervals for the fixed-effects estimate advocated by Richard Peto (1987) as the ‘typical effect’. Note that the vertical axis is on a logarithmic scale and that the hazard ratio scale on the right is flipped: smaller values at the top mean smaller risk in the BCG vaccinated group and therefore larger vaccine efficacy.

No futility analyses were planned in this collaboration, but the 30% vaccine efficacy prescribed by the FDA for COVID-19 trials (FDA, 2020) could have been a good candidate for a futility margin and 2,5% a good significance level for the type-I error guarantee for such a strong futility analysis. Using this margin in hindsight in Figure 7, a futility conclusion could have been drawn as early as December 2020/January 2021, when none of the values in the black ALL-IN confidence interval were larger than 30% vaccine efficacy. At this point, the collaboration could have advised against starting new trials or extending recruitment in ongoing trials, and the AF trial (the last one to start recruitment around that time) might have seen that coming and been able to change course. So collaboration in ALL-IN meta-analysis can reduce research waste by providing a leading source of information for all trialists to adjust their aims and optimize the value of their trial.

3.3 Collaboration in a competitive field or a pandemic: type-I, type-II errors and publication bias

Prospective ALL-IN meta-analysis prevents losing type-I error control when many trials compete for answers on the same research question, e.g. in a competitive field or an uncoordinated scientific response to a pandemic. If trials are only evaluated in isolation and a response follows the first positive result of a single trial, serious multiple testing issues arise that inflate the type-I error and result in unreliable inference and, subsequently, poor decisions. This happens especially if all trials perform interim analyses on their own, and a type-I error occurs at an interim analyses before any other trial results are published to refute it.

The example dashboard also clearly demonstrates decreased type-II errors: synthesizing the evidence in a meta-analysis at interim stages of the trials, and not after trials are completed, improves the ability to find an effect early. The COVID-19 pandemic showed that many individual studies can also be “at risk of failing to meet recruitment targets” (Petkova et al., 2020). A prospective meta-analysis on interim data can “honor the participation and risk assumed by the cohorts of study participants who deserve the maximal opportunity to have their participation result in useful findings” (Petkova et al., 2020).

In ALL-IN-META-BCG-CORONA, one trial had such difficulty recruiting participants, that the resulting findings ended up too noisy to merit a standalone publication (HU, see Table 1). Because the ALL-IN approach does not rely on stopping rules based on number of participants/events, this trial could still be included following the same analysis plan based on only 10 participants, as it would have with 950 participants. So recruitment difficulties do not change the position of a trial in a prospective meta-analysis and therefore do not change the standing of the research team in consensus discussions. Their knowledge and experience is optimally shared, and their data is published as part of the meta-analysis, so avoids publication bias.

3.4 Fixed-effects instead of random-effects meta-analysis

Sutton et al. (2007, p. 2491) note that “in a meta-analysis with considerable heterogeneity, the impact of a new (large) study will be (much) less in a random compared to fixed effect model”. This is due the incorporation of a parameter in the model that represents the between-study variation. Also Kulinskaya & Wood (2014) find that the goal of sequentially updating a random-effect meta-analysis might involve planning a large number of small trials to estimate the between-study variance well. Even if that is considered advisable, a random-effects model result might still be very difficult to interpret (Riley et al., 2011). Hence there are various reasons to prefer the fixed-effects model to monitor evidence efficiently and to ensure that the trials are sufficiently homogeneous.

Alongside the ALL-IN-META-BCG-CORONA analysis in healthcare workers we initiated a second ALL-IN meta-analysis that included trials in the elderly. Early in the process, before seeing any data, our Steering committee noticed that the two groups could be very different. Based on a theory of innate and trained immunity, they expected a different effect of the BCG vaccine on the younger immune system of healthcare workers than on the older immune system in the elderly. It could even be that the BCG vaccine effect was beneficial in the ability to fight off COVID-19 in one population but harmful in the other. In terms of statistical approach, the differences between trials can be in three categories: heterogeneous effects, conflicting effect and trial subgroup multiple testing.

Heterogeneous effects Our Steering committee decided that to declare success, all included trials in health-care workers should observe an effect of 20% VE or larger. If they indeed do, heterogeneity in their effect sizes (e.g. one 20%, one 50%, one 25%) does not matter for their joint ability to reject the global null hypothesis of no effect in all trials. So for testing the global null, trials are allowed to be heterogeneous in the space of the alternative hypothesis H₁ = {VE: 20% ≤ VE ≤ 100%}. For estimation, however, it is not clear what the ALL-IN confidence interval is estimating if we assume that the effects in the trials are very different. Still, as a first summary, a typical effect size (Peto, 1987) might be useful if we are unable to estimate a random effects model. The development of anytime-valid confidence intervals for random-effects meta-analysis is a major goal for future work. We do not, however, believe that the evidence in a line of research should be monitored based on whether this interval excludes the null hypothesis, or whether the e-value corresponding to the random-effects null model does: for testing, the global null is much more natural. Waiting for a random-effect model to reach a certain threshold is counter-intuitive, since it might require many small trials to estimate the between-trial variability instead of focusing on testing the treatment effect. Moreover, the goal of rejecting the null hypothesis corresponding to this model can be quite strange. When testing a zero-effect null hypothesis, it assumes that there are true effects of harm and true effects of benefit among the trials and that their mean is exactly zero.

Conflicting effects If one of the trials has an effect smaller than 20% or even a harmful effect, we should anticipate betting scores or e-values that are smaller than 1. So a meta-analysis multiplication of those e-values would reduce the evidence available from other trials. If we can identify groups for which we expect that the trials in each group have an effect in the same direction and of at least the minimal size, we can perform separate meta-analyses. This was the rationale behind grouping healthcare workers and the elderly each in their own ALL-IN-META-BCG-CORONA analysis.

Trial subgroup multiple testing When our analysis is exploratory, and we really have no idea how to group the various trials, we are faced with a multiple testing problem. Note that in this situation also no conventional meta-analysis method would be used to test a common null-hypothesis. We wonder whether any of the trials has the ability to reject the null hypothesis. In that case, we can divide our initial investment over the trials, and see if the totality of their bet achieves a high betting score. Research into this use of e-values has shown that indeed averaging e-values is the optimal way to have type-I error control in a standard multiple testing setting (Vovk & Wang, 2021) but there are many more advances in this area even improving upon p-value based methods for false discovery rate control and family-wise error rate control (Goeman et al., 2025; Ren & Barber, 2024; Wang & Ramdas, 2022; Xu et al., 2025). We return to the notion of hedging bets and averaging e-values in Section 4.

Problems with heterogeneity in meta-analysis are not tied to the ALL-IN approach and familiar to anyone working with meta-analysis methods. ALL-IN-META-BCG-CORONA had the advantage that many of the trials that started later had drawn inspiration from the protocol of the first trial. The same sort of alignment of inclusion criteria and outcome definitions might be achieved in other lines of research as well. Hence close collaboration can be very important and the promise of an early conclusion of the research effort might keep a research field motivated to keep the goals aligned.

4.1 The language of betting for two-sided tests

Our examples so far covered one-sided tests, but those can be easily extended to two-sided tests, e.g. by taking

to represent a two-sided alternative hypothesis

Such a two-sided test is easy to interpret in the language of betting. We essentially split our initial investment (e.g. €1) between the two sides of the alternative hypothesis (e.g. by betting €0.50 on one side and €0.50 on the other). Any other weighting of the two sides is also possible and corresponds to a different division of the initial investment. The crucial thing is that each side tests the same null hypothesis H₀ = { ϕ_µ0} and has expectation 1 under the null hypothesis, such that any weighted average also has expectation 1 and is an e-value. Note that for a meta-analysis at time t with k 〈t〉 studies this becomes:

Usually one side of the bet is losing and the other is winning such that we do not want to reinvest (multiply) across sides but keep them separate for all trials. In our ALL-IN-META-BCG-CORONA dashboard we also visualized these two sides of the meta-analysis test separately; in Figure 6 we show only the left-sided test (for benefit) of the two.

4.2 The language of betting for co-primary endpoints

Another way to hedge our bets is by considering multiple primary outcomes. In ALL-IN-META-BCG-CORONA, for example, not only were the COVID-19 events counted, but COVID-19 hospitalizations as well, as an indicator for severe disease. We started with α = 0.05 and put 10% on COVID-19 (α = 0.0025 on each of the two sides of a two-sided test) and 90% on hospitalizations (α = 0.0225 on each of the two sides of a two-sided test). So the thresholds to achieve with the e-value for COVID-19 was set at 1 /α = 400 and the one for hospitalization at 1 /α = 44.44. A different way to formulate this is that each had to achieve 1 /α = 20, but that the sequence of e-values for COVID-19 started with an initial investment of €0.05 for each side of the two-sided test (and had to multiply by 400 to reach €20) and that the e-value for hospitalization started with an initial investment of €0.45 for each side (and had to multiply by 44.44 to reach €20).

There are two ways to consider such a bet on two co-primary outcomes: separately and combined. If we evaluate the e-values for each primary outcome separately and reach the threshold with either of the two, we are rejecting the null for that outcome. We are doing two separate tests. If we evaluate the e-values combined, we average them weighted by their α, just as for the two sides of the two-sided test. In that case we have similar type-I error control, but reject the null hypothesis that both are a null effects in favor of the alternative hypothesis that one of them is not. Yet we cannot conclude which one is non-null with the same type-I error since our α-level applies to the combined bet and the individual components to the averaged bet are essentially lost.

Likelihood ratios, E-variables and e-values

In this paper we presented betting scores/e-values that are equivalent to likelihood ratios. In general though, betting scores and e-values are really generalizations of likelihood ratios that preserve the properties of likelihood ratios that give them a prominent role in statistics. Entire books have been written to advocate for summarizing evidence in observed data by a likelihood ratio (Edwards, 1974; Royall, 1997) and to separate the goal of measuring evidence from expressing posterior beliefs and making decisions. Likelihood ratios have the property that they can “favor a true hypothesis over a false one more and more strongly” and while a likelihood ratio can be misleading, “strong evidence cannot be misleading very often” (Royall, 1997, p. 14). This latter type-I error control is also referred to as a universal bound by Royall (1997) and, by recognizing Ville’s inequality, can be generalized to other betting scores and e-values.

A betting score € is a random outcome of a bet and its random variable is an E-variable if it is nonnegative and for all P ∈ H₀, E_P [€] ≤ 1. For a given outcome of the bet, the value of such a random variable is the e-value. Ville’s inequality relies on the multiplication of E-variables—forming a test martingale—which also has expectation smaller than 1 and thus is itself an E-variable. For the example e-values in this paper, the requirement on the expectation E₀[LR] ≤ 1 holds for a simple null hypothesis, e.g. H₀ = {ϕ₀}. Apart from likelihood ratios of two simple hypotheses, e-values can also be defined for more complicated tests—e.g. a t-test with a nuisance parameter for the variance—in which case the unit expectation needs to hold not for a single mean-0-normal distribution with known variance, but for all mean-0-distributions with any variance. Grünwald et al. (2024a) shows that it often is possible to construct E-variables for such composite testing problems, which is why we consider the e-value the right generalization of the likelihood ratio.

Anytime-valid confidence intervals

In this paper we presented anytime-valid (AV) confidence intervals (in Figure 3, Figure 8 and Figure 9) for the hazard ratio or VE that are based on the Gaussian approximation on the maximum likelihood estimator of the hazard ratio (for details, see the Statistical Appendix of Ter Schure et al., 2022). Research into other AV confidence intervals for the hazard ratio is still ongoing. For other estimation problems, AV confidence intervals already have been thoroughly studied, for example for medians and other quantiles (Howard & Ramdas, 2022), Gaussian means (Wang & Ramdas, 2025), odds ratios and risk differences (Turner et al., 2024) and estimates of multinomial count data (Lindon & Malek, 2022). These have not, however, been extended to meta-analysis, and especially for the random-effects meta-analysis model, research into AV confidence intervals is a major goal of future work.