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# Does donation matching work?

Note: in April 2015, 50% of the impact of this post was purchased by Paul Christiano and Katja Grace.

In the effective altruism community, donation matches are becoming very popular. Some matchers have gone as far as tripling or even quadrupling each dollar donated, not just doubling. But I started to wonder if the matching multiple—or even matching at all—has any impact on the money you raise. In this post, I’ll take a look at some of the academic literature on donation matching to see whether such matches are justified.

Thanks to Anders Huitfeldt and Elizabeth Santorella for looking over this review before publication. Any errors are entirely my own.

Note: this got fairly long. If you trust my analysis (which you shouldn’t!) and want the TL;DR, you can jump straight to the conclusion.

Contents

## Background and terminology

Like most research questions, it’s not totally clear what we actually want to measure.

The thing we ultimately care about is probably average revenue, the average amount of money you receive (not counting the match) per person you ask for donations. For instance, if you send a letter to 100 people, 10 of them donate $10 each, and 90 of them don’t respond, then your average revenue is$1.

Average revenue is the most important number for a given campaign, because it’s directly related to the amount of money you raise. However, as the discussion above suggests, it’s sometimes helpful to decompose average revenue as follows:

$$\textrm{average revenue} = \textrm{probability of donating} \times \textrm{average size of a donation}$$

We’ll call the terms on the right-hand side propensity to donate and average gift size.

Since different campaigns have different base rates (without the match) for propensity and gift size, I prefer to measure relative rather than absolute differences in propensity and gift size, to get a more apples-to-apples comparison.1

For propensity, I will sometimes report the relative risk—that is, the probability of donating with the match, divided by the probability of donating without the match. For gift size, I will report the gift size ratio, which is what it sounds like. In either case, I will report a point estimate followed by a two-standard-error interval in parentheses, as in 1.23 (1.07-1.39).

## Research methodology

Studies on donation matching fall into two broad categories: lab studies and field studies. Here I focus on field studies, because they tend to have larger samples, be less susceptible to publication bias, and have more realistic conditions. This can be important: for instance, “matching” donations by rebating half of each donor’s gift seems to be more effective in the lab (where the rebate is instantaneous) than in the field (where it takes longer and is more of a hassle).

I didn’t do a formal meta-analysis-style literature search, because I wanted to actually finish this post. However, I did search Google Scholar for the queries nonprofit donation matching, donation matching -kidney, and variants, and looked through the first three pages of results for randomized field studies of donation matching that had a freely-available PDF somewhere. After this I felt I was hitting diminishing returns on the literature search, so I stopped. (If you know of any additional studies that look at this phenomenon, please send me references and I’ll update this post!)

### Analysis

One issue with donation matching is that the baseline propensity to donate with no match is very low (typically on the order of 1%). This means that studies need to have very large sample sizes (tens of thousands) in order to have tight confidence intervals around their estimated effect size, and some of the field studies ended up with very low power.2

Another issue is that different fundraising campaigns are highly heterogeneous, that is, they have very different baseline propensities to donate and gift sizes. As a result, it’s most informative to look at relative effects of a matching challenge, like the relative risk for propensity to donate, or the percentage difference in gift size.

Unfortunately, most of the papers in my sample did not discuss their statistical power, or report their results in a way that made it easy to investigate. As a result, I had to back out many of these measures myself from tables in the papers. To calculate the relative risk and confidence interval, I used this spreadsheet.

## Priors

For transparency, I should state what I expected to find going into this study. Obviously, I tried not to let it bias my interpretation of the evidence, but I can’t make any promises. I wrote most of this section before conducting the review, but accidentally deleted the first section during editing and had to rewrite it. I also edited the second section for style after conducting the review.

### Does matching amount matter?

A naive economic model would predict that yes, the matching amount matters: a donation is essentially purchasing a good, and matching decreases the price of the good, so it should change demand and hence total consumption.3

However, I think this is unlikely to be true for a couple reasons.

• People suffer from scope neglect in donations, and so don’t really think about what the “price” of a donation is per se.

• Donations are sometimes used as costly signals, in which case it’s how much you pay that matters, not how much you buy.

As a result, I expect not to see very large effects from changing the matching ratio.

### Does matching help at all?

Despite the above, I do expect to see effects from the existence of a match, because of social proof and urgency effects. I expect this mostly to manifest in larger numbers of donations, rather than larger amounts per person.

However, I expect a lot of heterogeneity in results/effect sizes, because it matters a lot how the match is presented. Properly used, you can probably get a lot of leverage from a match, but it’s also possible to mess up the presentation and have it not be that influential.

## Results

I found seven studies of field experiments on donation matching. Unfortunately, many of them had significant flaws, either in design, implementation or analysis. Three (Meier 2006, Karlan et al. 2011, and Eckel and Grossman 2008) had potential randomization issues. Two (Meier 2006 and Karlan et al. 2011) raised concerns of specification searching. One (Rondeau and List 2008) was seriously underpowered. Two (Meier 2006 and Martin and Randal 2009) suffered from unusual designs that made the results hard to compare to other studies. Only two trial (Karlan and List 2007 and Eckel and Grossman 2007) did not raise significant concerns.

The table below summarizes general notes on each study. I go into more detail on individual studies after this section. “Weight” indicates how important I consider that study in drawing general conclusions (higher is better). For complete justification of these weights, check the appendix below.

StudySettingNMatchesWeight
Martin and Randal 2009Art museum donation box72 clusters100%3
Meier 2006Time series of student donations1,00025%, 50%2
Karlan and List 2007Direct mail50,000100%-300%4
Karlan et al. 2011Direct mail20,00025%, 100%1
Eckel and Grossman 2007Direct mail15,00025%, 33%4
Eckel and Grossman 2008Direct mail400,00025%, 33%2
Rondeau and List 2008Direct mail1,5004100%2

### Does matching help?

There seems to be moderate evidence that the existence of a donation match has an effect, but that effect is often lower than one would naively expect.

People’s general impression of matching seems to be that it about doubles non-match revenue. For instance, Charity Science wrote in their recap of a matching campaign:

Overall the match was extremely valuable. We feel that about half of all the donations made were significantly affected by the match. Many people actively commented that they were donating because of it. Because of this we will likely aim to have a match running for every major event in the future.

(I don’t mean to pick on Charity Science here! I quote them only because they stuck their necks out the farthest by naming a specific percentage. I think this view is not uncommon. I probably would have guessed something similar before reading the literature, although unfortunately I didn’t commit myself to an effect size when writing down my priors. Lesson learned!)

By contrast, the following table summarizes the effects I found. Unless otherwise noted, I pooled all match levels and all non-matching treatments (the differences between them were generally small).

Martin and Randal 20091.9%1.07 (no CI available)$2.111.2 (no CI available) Karlan and List 20071.8%1.22 (1.07-1.39)$460.96 (0.84-1.09)
Karlan and List 2007, blue states2%1.05 (0.89-1.24)$450.95 (0.8-1.1) Karlan and List 2007, red states1.5%1.53 (1.22-1.93)$470.97 (0.76-1.17)
Eckel and Grossman 20073.7%0.99 (0.83-1.18)$511.42 (1.32-1.52) Eckel and Grossman 20080.5%1.05 (0.92-1.2)$471 (1-1.01)
Rondeau and List 200854.6%1.05 (0.66-1.68)$281.23 (0.9-1.56) The three studies I give the most weight—Martin and Randal 2009, Karlan and List 2007, and Eckel and Grossman 2007—all found significant effects of matching on revenue, but more like 20-50% than 100%. The latter two studies had enough power to strongly rule out a 100% increase. Interestingly, though, they found it through opposite avenues. Martin and Randal and Eckel and Grossman 2007 found no effect on propensity to donate, but a 20-50% effect on gift size; the confidence interval for the latter was 1.42 (1.32-1.52).6 Meanwhile, Karlan and List 2007 found no effect on gift size (estimated gift size ratio 1.04 (0.97-1.11), ruling out an effect size of 1.2 with something like 99% confidence). On the other hand Karlan and List 2007 found a donation risk ratio effect of 1.22 (1.07-1.39). The confidence intervals for Eckel and Grossman 2008 included the low end of this range. Of course, some and potentially all of this is explained by heterogeneity. Martin and Randal’s experiment used a donation box in an art museum, whereas Karlan and List 2007 tested a direct mail campaign for a liberal nonprofit. Notably, even within the Karlan and List 2007, the benefit from matching was entirely absent in blue states (where Kerry won in 2004; risk ratio 1.05 (0.89-1.24)) but a very large effect in red states (risk ratio 1.53 (1.22-1.93)). Of the shakier studies, one other piece of evidence stands out: Meier 2006 found that donation matching increased donations in the short run, but decreased donations in the long run, so that the net effect of the match on money moved was negative. This is a little bit worrying, but Meier 2006 had a number of statistical issues and the matching scheme was unusual (see below for details), so I don’t put too much weight on this finding. I think it’s interesting and would love to see further research, but for now I’m not too worried that donation matching is net negative. Two other direct mail studies found lower or no effects of matching: Eckel and Grossman 2008 and Karlan et al. 2011. However, both of these studies had potential randomization issues (quite severe in the latter case) and the former tested only small matches, on the order of 30%. Additionally, in the Eckel and Grossman 2008, many donors’ donations were exactly equal to the organization’s membership fee, which was unaffected by the match, suggesting that donation amounts were largely influenced by personal benefits, rather than the good done by the donation. As a result I have serious doubts about how well these results would generalize. ### Does level of matching matter? The evidence here is much more ambiguous. The following table summarizes the findings of the four relatively sound studies that analyzed this (I exclude Meier 2006 because of my concerns about design and analysis). In each case, “baseline” refers to the lowest nonzero match group, and I compare to the highest (i.e., 300% vs 100% for Karlan and List 2007 and 33% vs 25% for Eckel and Grossman’s studies). StudyBaseline propensityPropensity ratioBaseline gift sizeGift size ratio Karlan and List 2007, all states2.1%1.1 (0.92-1.31)$450.92 (0.68-1.15)
Karlan and List 2007, blue states2.1%1 (0.79-1.27)$430.93 (0.73-1.12) Karlan and List 2007, red states2.1%1.24 (0.94-1.63)$480.91 (0.64-1.17)
Eckel and Grossman 20073.4%1.17 (0.95-1.45)$750.93 (0.86-0.99) Eckel and Grossman 20080.6%0.76 (0.61-0.96)$500.9 (0.89-0.9)

The most confident inference I can draw from these results is that there’s strong evidence of heterogeneity, caused in part by the different match levels, different organizations and different subject groups. Only Karlan and List 2007 tested reasonably large differences in matching schemes, so I place the most weight on their findings (and am surprised that Eckel and Grossman 2007 observed such large effects).

There is little evidence on response rates in either direction. While Eckel and Grossman 2007 and Karlan and List 2007 found higher point estimates (the latter only in red states), both intervals included no effect; meanwhile, Eckel and Grossman 2008 found a significant negative effect on response rates, but were using such a small difference in matching that I doubt it’s generalizable. (They had other unexplained issues with response rates as well; see below.)

One thing that stands out is that no study found an increase in average gift amount and both of Eckel and Grossman’s studies found a significant decrease. Because of the issues with membership fees that I mentioned before, I don’t place that much weight on this finding, but I think it’s notable nonetheless. This suggests that, to the extent the economic explanation for giving under matches is correct (that is, the influence of the match comes because it changes the price of giving), the price elasticity of donations is less than one—that is, increasing matching is likely to displace more giving than it creates.

## Conclusion

I don’t think the evidence here is strong enough either to categorically rule out or categorically support donation matching schemes as a use of money. But I do think we can draw some conclusions from it.

• The effect of donation matching is relatively small, on the order of 20% (with high uncertainty). No studies observed effects greater than 50% in any subgroup they investigated. On the other hand, the methodologically sound studies do largely find effects of matching.

• There are probably diminishing returns to matching above 1:1. The evidence for increased response rates is weak, and the increases are small if they exist. There’s (similarly weak) evidence for decreased average gift size.7

• Donation matching is not guaranteed to be positive. No studies found strong, generalizable negative effects of donation matching. However, several found worrying hints: Meier 2006 found that may have decreased net long-run donations, Eckel and Grossman 2008 found that it decreased response rate among some donors (probably due to the study’s unfamiliar-looking fundraising appeal), and there’s weak evidence that higher matching levels can actually crowd out some donations.

• The effect of donation matching is likely swamped by other sources of variation. Before you start donation matching, make sure you’re raising money from the right audience and have optimized your fundraising appeals, because both of these made more of a difference than the match in several studies. In fact, the director of marketing in Eckel and Grossman 2008 said as much:

From conversations with Mr. Al Anderson, Director of Membership Marketing, an earlier change that was designed to make rejoining easier (merely adding a 1-800 number to the pledge form) resulted instead in a significant drop in their response rate of about the magnitude we observed for the treatment groups. Mr. Anderson’s hypothesis about the impact of the 800 number is that potential donors set the pledge card aside intending to call, then did not.

Martin and Randal 2009 similarly found that, for their museum donation box, whether the donation was requested on Sunday made much more difference than matching, with a 50% increase in donation size.

• The secondary effects of donation matching are ambiguous and poorly studied. Meier 2006 found that the net effect of their donation match on revenue was marginally significantly negative. We would also expect that part of the effect of matching fundraisers is to shift gifts away from unmatched fundraisers, but I couldn’t find any field studies of this effect.

• There may be other better ways for large donors to leverage their money. Here I studied matching, but there are other ways of using large donations in fundraising. For instance, a lab study suggests that using the large donation to “cover the charity’s overhead” (so that one can claim, e.g., “100% of your donation goes directly to people in need”) is more effective than offering a match. Evidence from Rondeau and List 2008 weakly suggested that announcing the big donation as seed money had a larger effect than matching, as did simply asking for more money (although the results were not significant because their power was very low).

• If you’re matching, study your own matching scheme! There was a huge amount of heterogeneity in these studies, and the effects of donation matching varied widely as a result. In particular, most of the studies were on relatively impersonal direct mail campaigns, but many matches “in the wild” are spread by word-of-mouth. To the extent to which matches are driven by social proof, we would expect changing the social context to change people’s response to the match (although it’s unclear in what direction). Anyway, the upshot is that information about how your own donor base would react to a matching offer is still really valuable.

All things considered, I would recommend looking into other ways of using large donations to raise funds (although there’s not enough evidence to compare them right now). I would also recommend not matching donations at a rate greater than 1:1, instead using the additional funds to run more 1:1 matching campaigns (at minimum) or run experiments on different fundraising strategies (ideally).

(Also, I would recommend writing up the results of any experiments you run! Evidence is thin on the ground here, so every bit helps!)

## Appendix: Overview of individual studies

### Eckel and Grossman 2007

The authors studied a direct mail campaign to 15,000 prospective donors to Lutheran Social Service of Minnesota. They offered a match of either 25% or 33% (or an equivalent rebate, or a control offer). I did not analyze the rebate arms of the study.

The data showed no significant difference between response rates of either matching arm or the control, or between the matching arms. The risk ratio of donation given any match (pooling the matching treatments) was 0.99 (0.83-1.18). The data suggested a possible (non-significant) increase in response rate for the 33% match over the 25% match; the risk ratio between the two was 1.17 (0.95-1.45).

The data showed a strong difference in gift size between each arm and the control; the estimated effect when combining the matching arms was 1.42 (1.32-1.52). Interestingly, there was a slight but significant decrease in donation size from the 33% arm compared to the 25% arm; the estimated effect was 0.93 (0.86-0.99).

I didn’t see any major issues with the design, implementation or analysis of the study. One possible source of heterogeneity is the fact that the charity was religious (in light of the heterogeneity reported by Karlan and List 2007). The authors found a negative relationship between religious attendance and likelihood of donation,8 but did not investigate its interaction with the matching offer.

### Eckel and Grossman 2008

This study offered a match of either 25% or 33% (or an equivalent rebate, or a control offer) to about 400,000 potential donors of Minnesota Public Radio. I did not analyze the rebate arms of this study.

Unfortunately, this study also showed randomization issues. Current donors to MPR were not equally allocated between the treatment and control arms. Furthermore, these donors showed a significant decrease in response rate in all treatment arms. The authors hypothsized:

[T]here are two factors that may have contributed. First, the treatment group received a mailing that was different from what they were accustomed to seeing. From conversations with Mr. Al Anderson, Director of Membership Marketing, an earlier change that was designed to make rejoining easier (merely adding a 1-800 number to the pledge form) resulted instead in a significant drop in their response rate of about the magnitude we observed for the treatment groups. Mr. Anderson’s hypothesis about the impact of the 800 number is that potential donors set the pledge card aside intending to call, then did not. In our case, because of their loyal support of the organization, a substantial portion of the Continuing target group may have felt an obligation to consider the subsidy carefully as well as to complete the online survey, and may have set the mailing aside, fully intending to complete it at a later time. This is in contrast to the other two groups (Lapsed Members and Prospects), who exhibit no parallel difference in response rates for the treatment v. control groups, and who likely have no parallel ‘loyalty’ impulse.

Whatever the reason, it seems likely that findings in this study from continuing donors would not generalize, so I restricted my analysis to individuals who had never before donated to MPR (the largest group in the sample, about 300,000 subjects). Unfortunately, this group was subject to another confounding factor, which is that MPR required a donation of $42 (regardless of matching level) to qualify for membership. About 75% of new donors donated exactly$42, so this suggests that donors may have been primarily motivated by the benefits of membership, which were not subject to the match.

Comparing the combined treatment arms to the control group of no match, the propensity risk ratio was 1.05 (0.92-1.2). The gift size ratio was 1 (1-1.01), mostly due to the large number of $42 donations. Puzzlingly, I found that the 33% match had a significantly lower response rate and gift size than the 33% match (risk ratio 0.76 (0.61-0.96)). I’m concerned that this may be due to poor copy writing or something, though. ### Karlan and List 2007 Karlan and List mailed 50,000 previous donors to a liberal political nonprofit with a matching offer of 0, 100%, 200%, or 300%. They found fairly large and significant effects of matching on propensity and revenue. The propensity risk ratio for all treatment groups combined was 1.22 (1.07-1.39). Breaking down by matching level, Karlan and List found no significant relationship between match amount and either propensity, revenue or gift size. Unfortunately, they didn’t report confidence intervals on effect sizes for dollars donated, or test for a dose-response relationship. For donation size, the difference between matching levels is no more than 10% in any case, and there is no trend in the means. So it look like this isn’t just an issue of low statistical power. The propensity risk ratio between the 300% and 100% match groups was 1.1 (0.92-1.31), which limits the plausible effect sizes there. Interestingly, Karlan and List found that the treatment effect only existed in red states. (This is relevant since they were testing donations to a political organization. The control group had a significantly lower response rate in red states—1.5% versus 2%—while the treatment group had about equal response rates of 2.1% vs 2.3%.) I’m not sure what the best explanation for this is; the authors don’t really advance any. It does suggest that response to matching could be more situation-dependent than one would expect. When restricting to red states, the risk ratio of a 300% match compared to a 100% match was 1.24 (0.94-1.63)—still not significant, but this doesn’t rule out a reasonably large effect. On the other hand, for blue states that risk ratio was 1.00 (0.79-1.27).9 ### Karlan et al. 2011 This study compared 33% and 100% matches to a control group of no match for a sample of 20,000 previous donors to a “liberal organization that… focuses on civil justice issues.” They found overall no effect of either match compared to the control, on either propensity or gift size. Breaking the donors down into recent vs. non-recent donors (with a cutoff of 10 months), they found that the match made recent donors more likely to donate, and non-recent donors less likely to donate, with the effect being driven by the 33% match. The authors also reported several effects based on interactions between multiple factors: [W]e find that when the example matching amount is$25 instead of $1 (i.e., “For example, if you give$75, the matching donor will give $25” versus “For example, if you give$3, the matching donor will give $1.), then the ratio of the match does matter, in particular for those who have not given before. In this case, the larger example amount actually causes harm, whereas the aggregate effect is nil. I’m mildly skeptical of the various heterogeneity findings, since it’s possible that the authors tested other heterogeneity hypotheses but didn’t report the insignificant ones. This makes it likely that $p < 0.05$ is not a sufficiently strict threshold to limit false positives. Furthermore, they found a stronger effect ($p < 0.01$) on total donations after the match was supposedly over (although this effect disappeared when predicting log-donations instead of donations, which is otherwise a more reasonable specification). This raises some concerns that something went wrong with their mailing or something, which the authors don’t really investigate. The study’s randomization was also completely bonkers, with 5 of their 8 baseline variables significantly correlated with the “random” group assignment. The authors don’t discuss what caused this abject failure of their randomization scheme, which raises additional red flags. Ultimately, because of these statistical issues, I give this study limited weight, and mostly consider only the main finding. Because of the randomization issues, the authors had to control for all of these factors in their subsequent analysis, which meant I wasn’t able to extract confidence intervals on the propensity or gift size effects. ### Martin and Randal 2009 This study was a cluster-randomized trial of donations in an art museum. They left a donation box seeded with either$50 or $200 in the museum, with a sign saying “thank you” or informing visitors their donation would be matched (or no sign as a control). Unfortunately, they didn’t report confidence intervals, only p-values and sometimes point estimates. They found no significant effect on donation propensity, but highly significant effects on average donation size and average revenue per visitor (they didn’t give point estimates for the relative increase of these two, but it looks like it would be on the order of 0.1 to 0.3). Unfortunately, due to the cluster-randomized study design, I was unable to extract confidence intervals on either donation risk ratio or gift size ratio. ### Meier 2006 This paper studied students at the University of Zurich, who have the option to contribute to two funds every semester while paying tuition. The students were offered no match or a match of 25% or 50%. The experiment was unique in that the students had the chance to donate every semester, so the authors were able to look at the long-run effects of the match. They found that treatment increased short-run contributions, but decreased long-term contributions—apparently, students decreased their donation after the match ended to levels lower than before it began. Breaking down by match level, they found that the 25% match was not effective, but the 50% match was. This match had a slightly weird structure: students were asked to donate to two different funds (each one by checking off a checkbox on their tuition form), but the match only applied if they donated to both. Because this ended up discretizing the problem weirdly, I’m not sure how well the study will generalize (for instance, if there had been no maximum contribution, or if going from$0 to $4 had allowed you to take advantage of the match, students might have increased their donations more). Additionally, contribution rates before the match were already high (almost 70%) at baseline, making the likely effect smaller than a typical field study. For instance, it would have been literally impossible for Meier to observe a relative increase as large as the one Karlan and List 2007 observed in red states. Another caveat is that even though the study was randomized, it appears to have been confounded by mismatched contribution levels between the study groups at baseline. Thus the authors resorted to a difference-in-differences analysis of time series, rather than a naive model. Although in theory this should be fine (and in fact lower-variance than a naive model), it raises concerns about specification search. Meier reported some results from the naive model and some results from the differences-in-differences model, but none of their results appeared to be robust between the two. Surprisingly, Meier claimed to find that in the long run the match had a net negative effect on average donation per student. However, this result was only significant in the (confounded) naive model; it was just marginally significant ($p < 0.1$) in the differences-in-differences model. So we should interpret the result cautiously. In the end, because of various issues with a strange matching structure and possibly poor randomization/specification searching, I place almost no weight on this study. ### Rondeau and List 2008 These authors studied a direct mail campaign to 3,000 supporters of the British Columbia Sierra Club. The study’s power was too low to be informative, unfortunately: it couldn’t have distinguished a 30% increase in donations from noise. The study had four experimental groups, two control and two intervention (a match and a “challenge”). In the “low control group” they asked for the same amount as in the intervention groups ($2500), which meant they were asking for half the total amount they claimed they wanted in the other groups (since the matching/challenging donor was providing half the funds); in the “high control group” they asked for twice as much (so the entire amount that they told the other groups they wanted to raise).

In order to disentangle the effect of matching from the effect of the larger “ask,” I compared the matching group to the “low control” group. Here the propensity risk ratio was 1.05 (0.66-1.68), and the gift size ratio was 1.23 (0.9-1.56).

Interestingly, the study found that both the challenge gift and the “high control” group had significantly higher gift sizes than the “low control” group. (The revenue difference between high and low control was not significant, because non-significantly fewer people donated in the low control group; nor was either group significantly different from the matching group.) This suggests that there may be less costly ways to increase donations than matching, but heterogeneity and wide confidence intervals mean that we shouldn’t put too much weight on that result.

Note that this study involved multiple comparisons (6 different tests for differences in pairwise means), and hence p-values should be taken with a grain of salt. Furthermore, and more egregiously, my version of the paper described the results of a Student’s t test as “Probability that the Mean of Individual Contributions in the [Two] Treatments are Equal,” giving me extremely serious doubts about their statistical acumen. As far as I can tell they didn’t make any actual mistakes in their analysis, but this kind of thing makes me pretty nervous that I missed something.

## Sources

Karlan, Dean and John A. List. 2007. “Does Price Matter in Charitable Giving? Evidence from a Large-Scale Natural Field Experiment.” American Economic Review, 97(5), 1774-1793. [PDF, NBER, notes]

Eckel, Catherine C. and Philip J. Grossman. 2008. “Subsidizing charitable contributions: a natural field experiment comparing matching and rebate subsidies.” Experimental Economics, 11(3), 234-252. [PDF, SSRN, notes]

Eckel, Catherine C. and Philip J. Grossman. 2007. “Encouraging Giving: Subsidies in the Field.” Working paper. [PDF, SSRN, notes]

Rondeau, Daniel and John A. List. 2008. “Matching and challenge gifts to charity: evidence from laboratory and natural field experiments.” Experimental Economics, 11(3), 253-267. [PDF, NBER, notes]

Meier, Stephan. 2006. “Do Subsidies Increase Charitable Giving in the Long Run? Matching Donations in a Field Experiment.” FRB of Boston Working Paper #06-18. [PDF, SSRN, notes]

Martin, Richard and John Randal. 2009. “How Sunday, price, and social norms influence donation behaviour.” The Journal of Socio-Economics, 38(5), 722-727. [PDF, notes]

Karlan, Dean, John A. List, and Eldar Shafir.* 2011. “Small Matches and Charitable Giving: Evidence from a Natural Field Experiment.” *Journal of Public Economics*, 95(5-6), 344-350. [PDF, notes]

## Footnotes

1. Of course, ratios are not completely apples-to-apples; it’s easier to convince someone to double a gift of $1 than a gift of$100. So I also report base rates and try to determine whether lower base rates are associated with higher effect sizes. ↩

2. Although absolute confidence intervals are smaller for very low (or very high) base rates, relative confidence intervals are larger, so for a fixed relative risk, low base rates make differences harder to detect. For instance, it’s a lot easier to detect a risk ratio of 2 if the base rate is 25% than if the base rate is 0.1%. For the first one you can easily see the difference with 20 subjects in each arm, but for the second one you need 600 subjects in each arm to have even odds of getting even one positive case. ↩

3. One can produce models where this isn’t true—if the price elasticity of donations lines up just right with the consumer’s utility function, then donations getting cheaper can be exactly offset by diminishing marginal returns to donations, such that if the price of a donation falls by (say) 50% then the consumer purchases exactly twice as many donations, and net spending stays exactly the same. However, this would be a surprising coincidence. ↩

4. The study’s full sample was 3,000, but I only looked at two of their four subgroups; see the study section below for more details. ↩

5. This compares only the matching arm to the “low control” arm; see study notes for details. ↩

6. I couldn’t calculate a confidence interval for Martin and Randal 2009 because the trial was cluster-randomized and did not report confidence intervals (only p-values). ↩

7. Note that this doesn’t necessarily mean that each individual donor’s contribution was decreased by the match. Instead, it could be the case that a 2:1 match has no effect on gift size, but causes some additional people to donate at a lower gift size who wouldn’t have donated at all in a 1:1 match. ↩

8. The authors found a positive relationship between attendance and reported annual giving, though, suggesting that donations to Lutheran Social Services were crowded out by donations to the church. ↩

9. It’s exactly equal to 1 because I’m backing out the donation counts from reported response rates, which were exactly equal between the two groups. ↩

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This post is pretty long and the comments might get gnarly, so please comment on the EA forum post instead of here! (I’m going to delete comments here to make sure all the threads stay in one place.)

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CAS.Beta(number, number)

Home - RPN Entry

2: number 1: number CAS.Beta(2), press Enter

CAS Mode

Beta(number or algebraic expression, number or algebraic expression)

Numbers can be real or complex.

Output:

Beta(x,y) = (x-1)! * (y-1)! / (x+y-1)!

Examples:

Beta(8,5) returns 1/3960

Beta(1+7*i, -2*i) returns .00118622003099-.0037324363508*i

Access: Toolbox, Math, 8. Special, 1. Beta

#### Gamma

Calculates the gamma function. Gamma(x) = integral of t^(x-1) * e^-t dt from 0 to infinity

Also Gamma(x) = (x-1)!

Syntax

Input:

Home - Algebraic Entry Home - Textbook Entry Program Editor

CAS.Gamma(number)

Home - RPN Entry

1: number CAS.Gamma(1), press Enter

CAS Mode

Gamma(number)

Output : Result of the Gamma function. See the formulas above.

Notes: Gamma for complex numbers work best in CAS mode. Factorial and gamma of complex numbers in Home mode cannot be approximated.

Examples:

Gamma(5) returns 24 Gamma(-8) returns Inf in Home Mode, ±∞ in CAS Mode

Related: Psi, Beta

#### Psi

The Psi returns the nth derivative of the digamma function. The digamma function is defined as:

Ψ(x) = d/dz ln Γ(x)

The general syntax of Psi is Psi(number, order). If order is omitted, then digamma function is calculated.

Syntax

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.Psi(number, order)

Home - RPN Entry

2: number 1: order CAS.Psi(2), press Enter

For the digamma function: 1: number CAS.Psi(1), press Enter

CAS Mode

Psi(number, order)

Output: Result of the polygamma function. See the formulas above.

Examples:

Digamma: Psi(6) returns -euler_gamma + 137/60, approximately 1.70611766843

Polygamma: Psi(6,2) returns -2 *(Zeta(3) - 256103/216000), approximately -.032789732245

Notes: euler_gamma is the gamma constant, which is approximately 0.577215664902.

Access: Toolbox, Math, 8. Special, 3. Psi

#### Zeta

Calculates the Zeta (ζ) function. The general formula for the Zeta function is:

ζ(x) = Σ (k^-x) from k = 1 to ∞

Syntax

Zeta(real number).

Caution: Complex numbers return a result with the Eta function, which does not give full approximate answers. (rev. 5166)

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.Zeta(real number)

Home Mode - RPN Entry

1: real number CAS.Zeta(1), press Enter

CAS Mode

Zeta(real number)

Output: Result of the zeta function. If the number is an even integer, an exact answer is returned. If the number is an odd integer, Zeta(odd integer) is returned, which can be approximated. Otherwise, an approximate answer is returned.

Examples:

Zeta(3) returns Zeta(3),which is approximately 1.20205690316 Zeta(6) returns π^6/945, which is approximately 1.01734306198 Zeta(3.25) returns 1.15915198568

Access: Toolbox, Math, 8. Special, 4. Zeta

#### erf

Calculates the error (erf) function. The general formula for the error function is:

erf(x) = 2/√π * ∫ e^(-t^2) dt from 0 to x

Syntax

erf(number)

The number can either be a real or complex number.

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.erf(number)

Home Mode - RPN Entry

1: number CAS.erf(1), press Enter

CAS Mode

erf(number)

Output: Result of the error function.

Home Mode: erf(number) is returned.

CAS Mode Only: If the number is an integer, erf(integer) is returned, which can be approximated. If the number is not an integer, an approximation is returned.

Examples:

CAS Mode: approx(erf(2)) returns .995322265019 approx(erf(3)) returns .999977909503

Access: Toolbox, Math, 8. Special, 5. erf

#### erfc

Calculates the error compliment (erfc) function. The general formula for the error compliment function is:

erfc(x) = 1 - erf(x)

Syntax

erf(number)

The number can either be a real or complex number.

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.erfc(number)

Home Mode - RPN Entry

1: number CAS.erfc(1), press Enter

CAS Mode

erfc(number)

Output: Result of the error complement function.

Home Mode: 1 - erf(number) is returned.

CAS Mode Only: If the number is an integer, 1 - erf(integer) is returned, which can be approximated. If the number is not an integer, an approximation is returned.

Examples:

CAS Mode: approx(erfc(2)) returns .00467773498105 approx(erfc(3)) returns 2.20904969837E-5

Access: Toolbox, Math, 8. Special, 6. erfc

#### Ei

Calculates the exponential integral: Ei(x) = ∫ e^-t/t dt from x to ∞

Syntax

Ei(number)

The number can either be a real or complex number.

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.Ei(number)

Home Mode - RPN Entry

1: number CAS.Ei(1), press Enter

CAS Mode

Ei(number)

Output: Result of the exponential function.

CAS Mode, Home Mode with Textbook or Algebraic Entry: If the number is an integer, then Ei(integer) or CAS.Ei(integer), respectively, is returned, which can be approximated. If the number is not an integer, or a complex number, then an approximation is returned.

Home Mode with RPN Entry: Ei(number) is returned if the number is an integer. Otherwise, an approximate answer is returned.

Examples:

CAS Mode: approx(Ei(2)) returns 4.954234356 approx(Ei(3)) returns 9.93383257063

Access: Toolbox, Math, 8. Special, 7. Ei

#### Si

Calculates the sine integral: Si(x) = ∫ sin t/t dt from 0 to t

Syntax

Si(number)

The number must be a real number. A “Bad Argument Value” error occurs when the argument is a complex number.

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.Si(number)

Home Mode - RPN Entry

1: number CAS.Si(1), press Enter

CAS Mode

Si(number)

Output: Result of the sine integral function.

CAS Mode, Home Mode with Textbook or Algebraic Entry: If the number is an integer, then Si(integer) or CAS.Si(integer), respectively, is returned, which can be approximated. If the number is not an integer, or a complex number, then an approximation is returned.

Home Mode with RPN Entry: Si(number) is returned.

Examples:

CAS Mode: approx(Si(2)) returns1.6054129768

Access: Toolbox, Math, 8. Special, 8. Si

#### Ci

Calculates the cosine integral: Ci(x) = euler_gamma + ln x + ∫ (cos t - t)/t dt from 0 to t where euler_gamma is the gamma constant, which is approximately 0.577215664902.

Syntax

Ci(number)

The number must be a real number. A “Bad Argument Value” error occurs when the argument is a complex number.

Input:

Home Mode - Algebraic Entry Home Mode - Textbook Entry Program Editor

CAS.Ci(number)

Home Mode - RPN Entry

1: number CAS.Ci(1), press Enter

CAS Mode

Ci(number)

Output: Result of the sine integral function.

CAS Mode, Home Mode with Textbook or Algebraic Entry: If the number is an integer, then Ci(integer) or CAS.Ci(integer), respectively, is returned, which can be approximated. If the number is not an integer, or a complex number, then an approximation is returned.

Home Mode with RPN Entry: Ci(number) is returned.

Examples:

CAS Mode: approx(Ci(2)) returns .422980828775

Access: Toolbox, Math, 8. Special,9. Ci

format: plain


text:
Derivative of the flow for ODEs on manifolds

Let $\mathbf V \colon [0,T] \times \mathbb R^d \to \mathbb R^d$ (for $T>0$) be a given, bounded smooth vector field and let $\mathbf X=\mathbf X(t,x)$ be its flow, i.e. the unique solution to the initial-value problem $$\begin{cases} \frac{\partial}{\partial t} \mathbf X(t,x) = \mathbf V(t,\mathbf X(t,x)) & \text{ in } (0,T) \times \mathbb R^d \\ \mathbf X(0,x) = x \quad \text{ for all } x \in \mathbb R^d. \end{cases}$$

A well-known result in standard ODE's theory says that $$\tag{1} \nabla_x \mathbf X(t,x) = \exp\bigg( \int_0^t \nabla \mathbf V(s,\mathbf X(s,x))\,ds\bigg).$$

Is there an analogous formula to (1) for ODEs driven by (smooth) vector fields on Riemannian manifolds? In particular, does this formula involve somehow the geometry of the Riemannian manifold? A rather precise question could be: consider the $C^1$ norm of $\mathbf X$ (or even its Lipschitz constant) w.r.t. space variable $x$: does it depend on some known tensors on the manifold (e.g. curvature)?

I have gone through books in differential geometry/differential topology (e.g. Lee, Lang) and they prove that $\mathbf X$ is smooth but do not compute explicitly the derivative.

References are very much welcome. Thanks.

• I suggest migrating this math.stackexchange.com – Deane Yang Oct 29 '17 at 16:42
• Anyway, the answer is do everything with respect to local co-ordinates. – Deane Yang Oct 29 '17 at 17:27
• When solving for integral curves (the flow) of a vector field on a manifold, no geometric structure (connection, metric, etc.) is needed at all. What you want to check is that any solution with respect to one set of local coordinates is also a solution with respect to any other set of local coordinates. – Deane Yang Oct 29 '17 at 19:32
• This is probably covered in any differential geometry or differential manifolds textbook. I suggest looking at Lee's book, Introduction to Smooth Manifolds. – Deane Yang Oct 29 '17 at 19:34
• A family of diffeos $\phi\colon M\to M$ lifts to a family $T\phi\colon TM \to TM$, the Jacobian of $\phi$, which is linear on the fibers of $TM$. The analog of the determinant here is the induced map $\Lambda^n T\phi\colon \Lambda^n TM\to \Lambda^n TM$ ($n=\dim M$). Differentiating both $T\phi$ and $\det T\phi$ with respect to the family parameter gives vector fields $TM\to T(TM)$ and $\Lambda^n TM\to T(\Lambda^n TM)$. The relation between the latter two should be a kind of "trace", though I don't know it's precise nature off hand. – Igor Khavkine Oct 29 '17 at 23:04

I think you may be interested in this remarkable, recent paper by E. Brué and D. Semola (see in particular Theorem 3.11 which answers to your question in a much more general setting).

As was pointed out by Deane Yang and Igor Khavkine in the comments, this feels like a fact that should be "looser" than Riemannian geometry. Indeed, as I will show below, your formula makes sense in the broader setting of smooth manifolds equipped with a volume form. I don't know a reference for this fact.

If $(M, \Omega)$ is a manifold equipped with volume form, ${\bf V}\in \operatorname{Vect}(M)$ is a vector field on $M$, and ${\bf X}_t:M\to M$ is the flow of ${\bf V}$, then:

1) One has $J_t\in C^\infty(M)$, (i.e., a smooth $J:\mathbb{R}\times M\to M$), with $J_0\equiv 1$, given by, $$J_t(x)=(\Omega_x)^{-1}\otimes \Omega_{{\bf X}_t(x)}\otimes \Lambda^n(d{\bf X}_t|_x),$$ well-defined since $\Lambda^n(d{\bf X}_t|_x):\Lambda^n( T_xM)\to \Lambda^n (T_{{\bf X}_t(x)}M)$ as Igor said.

2) One has a well-defined $\operatorname{div}({\bf V})$, namely (up to a sign, I forget whether $\pm$) $$\operatorname{div}({\bf V})=d(\iota_{\bf V}\Omega)/\Omega.$$

So the "hopefully-an-identity" $$\left.\frac{d}{dt}\right\rvert_{t=0}J_t=\operatorname{div}({\bf V})$$ (for simplicity I state just the $t=0$ formula) is well-formed. You can then prove it by choosing local co-ordinates in which $\Omega\equiv 1$. (There is surely an intrinsic proof, too, but I can't think of one now.)

Afterthought, 30 Oct: I imagine the intrinsic proof consists of identifying both sides with the Lie derivative $(\mathscr{L}_{\bf V}\Omega)/\Omega$.

Update, 30 Oct, in response to questions of OP in comments: If I calculate correctly, then yes, the formulas \begin{align*} \frac{dJ_t}{dt}(x)&=\operatorname{div}({\bf V})|_{{\bf X}_t(x)} J_t(x)\\ J_t(x)&=\exp\left(\int_0^t\operatorname{div}({\bf V})|_{{\bf X}_s(x)}ds\right) \end{align*} are also correct.

And yes, although the formula for "$\tfrac{d}{dt}\left[\det\left(d{\bf X}_t\right)\right]$" depends only on the volume form, I think one needs a Riemannian metric $g$ in order to make sense of "$\tfrac{d}{dt}\left[d{\bf X}_t\right]$" (really, the $g$-covariant derivative $D_t$ of the section $d{\bf X}_t$ of the bundle $T_x^*M\otimes TM$ along the curve ${\bf X}_t(x)$). Probably $$D_t\left[d{\bf X}_t\right]|_{t=0}=\nabla {\bf V},$$ where $\nabla$ is the Levi-Civita connection of $g$. (Please check this calculation before relying on it!)

• There is a corollary of this fact which, I think, is better-known: the flow of ${\bf V}$ preserves a volume form if and only if ${\bf V}$ is divergence-free with respect to that volume form. – macbeth Oct 30 '17 at 7:30
• @macbeth , Life is more complicated on the variational case : see my comments here mathoverflow.net/questions/277168/… we don't have uniqueness. – user21574 Oct 31 '17 at 1:10
• @user111164 You're welcome. Unfortunately I don't know references for these formulas (and therefore, by the way, I disagree with the designation of the question as "off-topic"). If there exists a book on dynamical systems specifically on Riemannian manifolds, that might be a good bet. The formulas might also turn up in a book on Morse theory, at least in the case $V=\nabla f$. – macbeth Oct 31 '17 at 13:07
• @DeaneYang There was a flag asking to consider reopening this question. In view of your apology in a comment above, do you think the question should be reopened? – Todd Trimble Feb 9 '18 at 12:41
• I've voted to reopen. – Deane Yang Feb 9 '18 at 16:10


text:
# Properties of the product and the quotient of the logarithms

Let's learn how to create and solve exercises based on the properties of the product and the quotient of the logarithms.

A property of the logarithms is: $$log_a (x\cdot y)=log_a x+log_a y$$

Or, in other words, the logarithm of the product of two numbers is the sum of the logarithms of these numbers.

$log_2 (8\cdot64)=log_2 8+log_2 64=log_2 2^3+log_2 2^6=3+6=9$

Also:

$log_5 (125\cdot625)=log_5 125+log_5 625=log_5 5^3+log_5 5^4=3+4=7$

When we have a product of logarithms we have to add, but when we have a quotient we have to subtract, therefore the second property of the logarithms is: $$log_a \dfrac{x}{y}=log_a x - log_a y$$

Or, in other words, the logarithm of the quotient of two numbers is equal to the logarithm of the numerator minus the logarithm of the denominator.

$log_3 \dfrac{9}{81}=log_3 9-log_3 81= log_3 3^2-log_3 3^4=2-4=-2$

Also:

$log_{10} \dfrac{0,001}{0,01}=log_{10} 0,001-log_{10} 0,01= log_{10} 10^{-3}-log_{10} 10^{-2}=-3+2=-1$

The base of the last example $(10)$ is very common. In fact, it is one of two types of logarithms that scientific pocket calculators calculate. It is called decimal logarithm and it is usually abbreviated as log, without any need to specify the base.

Another type of logarithm, very common as well, is the natural or neperian, which has number $e$ as its base and is abbreviated $ln$.

The properties of the product and the quotient of the logarithms can be used together in order to simplify expressions.

It is possible to group the following expression into just one logarithm: $$ln127-ln481-ln7+ln74$$ First, the elements with the same sign are grouped: $$(ln127+ln74)-(ln481+ln7)$$ Applying the properties of the product and the quotient, we obtain: $$(ln127+ln74)-(ln481+ln7)=ln(\dfrac{127\cdot74}{481\cdot7})$$

The following expression sums up the properties of the logarithms seen until now. We have to try to reduce the expression in just one logarithm: $$log10^{-2}-log\dfrac{3}{4}+log13^{\frac{1}{3}}-log5$$ First we group the elements with the same sign: $$\Big(log10^{-2}+log13^{\frac{1}{3}}\Big)-\Big(log\dfrac{3}{4}+log5\Big)$$

Now we apply the properties of the product, quotient and the power of a logarithm: $$\Big(log10^{-2}+log13^{\frac{1}{3}}\Big)-\Big(log\dfrac{3}{4}+log5\Big)=log\dfrac{10^{-2}\cdot13^{\frac{1}{3}}}{\dfrac{3}{4}\cdot5}=$$ $$=-2\cdot\dfrac{1}{3}log\dfrac{1\cdot13}{\dfrac{15}{4}}=-\dfrac{2}{3}log\dfrac{52}{15}$$

Notice that the product and quotient properties of the logarithms come from the corresponding properties of the powers: $$log_a (x\cdot y)=log_a x+log_a y$$ Because $a^n \cdot a^m=a^{n+m}$, and applying logarithms implies calculating $n$ and $m$.

On the other hand: $$log_a \dfrac{x}{y}=log_a x-log_a y$$ since $\dfrac{a^n}{a^m}=a^{n-m}$


text:
# Probability from decision theory

There exists a problem in the world, that is even more pressing than the position of cheese in the cheeseburger emoji: namely that nobody™ understands the Deutsch-Wallace theorem. I’ve talked to a lot of people about it, and the usual reaction I get is that they have heard of it, are vaguely interested in how can one prove the Born rule, but have no idea how Deutsch and Wallace actually did it.

It’s hard to blame them. The original paper by Deutsch is notoriously idiosyncratic: he even neglected to mention that one of his assumptions was the Many-Worlds interpretation[1]! Several people wrote papers trying to understand it: Barnum et al. mistakenly concluded that Deutsch was simply wrong, Gill made a valiant effort but gave up without a conclusion, and Wallace finally succeeded, formalising Deutsch’s proof and putting it in context.

Wallace was not successful, however, in popularising the theorem. I think this is because his paper is a 27-page mess. It did not help, either, that Wallace quickly moved on to improving Deutsch’s theorem, providing an even more complicated proof from weaker assumptions, leaving the community with no easy entry point in this confusing literature.

To fill this hole, then, I’m writing two “public service” blog posts. The first (this one) is to explain how to derive probabilities from decision theory, and the second is to show how this decision-theoretical argument, together with the Many-Worlds interpretation, yields the Born rule.

Unlike Deutsch, I’m going to use a standard decision theory, taken from the excellent “The Foundations of Causal Decision Theory” by James Joyce. We’re going to consider a simple betting scenario, where an agent decides how much to pay to take part in a game where they receive $a$ euros if event $E$ happens, and $b$ euros if event $\lnot E$ happens[2]. The game is then defined by the vector $(a,b)$, and the agent wants to decide its value $V(a,b)$.

The first rationality axiom we demand is that if the game is certain to pay them back $c$ euros, they must assign value $c$ to the game. This means that the agent is indifferent to betting per se, they don’t demand some extra compensation to go through the effort of betting, nor are they accept to lose money just go experience the thrill of betting (unlike real gambling addicts, I must say). The axiom is then

• Constancy: $V(c,c) = c$.

The second axiom we demand is that if for a pair of games $(a,b)$ and $(c,d)$ it happens that $a \ge c$ and $b \ge d$, that is, if in both cases where $E$ happens or $\lnot E$ happens the first game pays a reward that is larger or equal than the second game, then the agent must value the first game no less than the second game. The axiom is then

• Dominance: if $(a,b) \ge (c,d)$ then $V(a,b) \ge V(c,d)$.

The third and last axiom we need sounds very innocent: if the agent is willing to pay $V(a,b)$ to play the game with rewards $(a,b)$, and thinks that playing for rewards $(c,d)$ is worth $V(c,d)$, then the price they should pay for getting the rewards $(a+c,b+d)$ must be $V(a,b) + V(c,d)$. In other words: it shouldn’t matter if tickets for the game with rewards $(a+c,b+d)$ are sold at once, or broken down into first a ticket for rewards $(a,b)$ followed by a ticket for rewards $(c,d)$. The axiom is then

• Additivity: $V(a+c,b+d) = V(a,b) + V(c,d)$.

One problem with Additivity is that real agents don’t behave like this. People usually assign values such that $V(a+c,b+d) < V(a,b) + V(c,d)$, because if you have nothing then 10€ might be the difference between life and death, whereas if you already have 10,000€ then 10€ is just a nice gift. Besides not matching reality, this linear utility function implied by Additivity causes pathological decisions such as the the St. Petersburg paradox or Pascal’s Wager. But these problems do not appear if the amounts at stake are small compared to the agent’s wealth, which we can assume to be the case, and Additivity makes for a rather simple and elegant decision theory, so we’ll use it anyway[3]. After all, I’m not writing for the people whose objection to the Deutsch-Wallace theorem is that Deutsch’s decision theory implies linear utilities, but rather for those whose objection is “What the hell is going on?”.

Now, to work. First we shall show how Additivity allows us to write the value of any game as a function of the value of the elementary games $(1,0)$ and $(1,0)$. Additivity immediately implies that
$V(a,b) = V(a,0) + V(0,b),$and that for any positive integer $n$
$V(na,0) = nV(a,0).$Taking now $a=1/n$, the previous equation gives us that $V(1,0) = nV(1/n,0),$ or that $V(1/n,0) = \frac1n V(1,0).$ Considering $m$ such games, we have now that $V(m/n,0) = \frac{m}{n} V(1,0)$ for any positive rational $m/n$. We can extend this to all rationals if we remember that by Constancy $V(0,0) = 0$ and that by Additivity
$V(0,0) = V(m/n,0) + V(-m/n,0).$Now one could extend this argument to all reals by taking some continuity assumption, but I don’t think it is interesting to do so. I’d rather assume that one can only have rational amounts of euros[4]. Anyway, now we have shown that for all rational $a$ and $b$ we have that
$V(a,b) = aV(1,0) + bV(0,1).$What is left to see is that the values of the elementary games $(1,0)$ and $(0,1)$ behave like probabilities. If we consider Constancy with $c=1$ we have that $V(1,0) + V(0,1) = 1,$ so these “probabilities” are normalised. If we now consider Dominance, we get that
$V(1,0) \ge V(0,0) = 0,$so the “probabilities” are positive. Is there anything left to show? Well, if you are a Bayesian, no. The probability of an event $E$ is defined as the price a rational agent would pay for a lottery ticket that gives then 1€ if $E$ happens and nothing otherwise. Bayesians have the obligation to show that these probabilities to obey the usual Kolmogorov axioms, but on the interpretational side there is nothing left to explain.


text:
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text:
# Curves intended for both signing and key agreement

I need some guidance on elliptic curves that support signing and key agreement.

I am trying to develop a protocol for sending encrypted, deniably authenticated messages. To do this I will sign the message with a 2-key ring signature using the sender's signing key and the recipient's encryption key.

Is there a sensible elliptic curve to use for this? Ideally it would meet the safe curves standards and provide the same level of security as Curve25519 (i.e. 256 bit length / 128 bit security).

Ed448-Goldilocks looks like it fits the bill as a curve intended to support both functions but is there anything more lightweight?

• What's wrong with Curve25519? – SEJPM Jan 15 '17 at 22:36
• I don't know. That's one reason I'm asking the question. I'm having a hard time tracking down any literature that gives a good account of why there are separate Bernstein curves for signing (Ed25519) and key agreement (Curve25519). – geoff_h Jan 15 '17 at 22:47
• @geoff_h Ed25519 refers to a signature system. The curve it uses to create those signatures is isomorphic to Curve25519, so they are abstractly the same curve — only the representation is different. In any case, ring signatures seem overkill for your purpose: Once you have a shared key, can't you just use public-key authenticators, as is for instance done in NaCl's crypto_box? – yyyyyyy Jan 15 '17 at 23:11
• Ok. But can you point me at a rationale for using different isomorphisms? I believe you and it's my understanding as well but I'd like to understand the split before taking that route. Thanks. – geoff_h Jan 15 '17 at 23:19
• Nitpick: the curves are birationally equivalent, not isomorphic. – CurveEnthusiast Jan 16 '17 at 8:11

Technically, any elliptic curve can support both signing and key agreement. However, Curve25519 as described in the original paper is meant for $x$-only arithmetic. This means that one never computes the $y$-coordinate. The issue is that you need the $y$-coordinate for signature verification in the standard algorithms (ECDSA, EdDSA).
Therefore, if you want to do signatures with the Curve25519 curve, you need to compute the $y$-coordinate. There are different ways to do this, one is to simply leave the curve as is (in "Montgomery form") and compute its $y$-coordinate. A different way, is to transform the curve into a new shape (the "twisted Edwards form") and do arithmetic there. This new curve is called Ed25519, and it is "(birationally) equivalent" to the old curve. There are even more flavours.
Again, the choice you make will be for efficiency and security. Not because one curve can be used for signatures while the other can't. I suppose the $y$-coordinate computation on Curve25519 is slow enough for people to prefer using Ed25519 instead.
• A minor detail: computing the $y$-cordinate on Montgomery curves costs only about 13 Multiplications. The issue is that in verification you need a full point addition which is not present in the Montgomery ladder, so you need to add code for that, and it has exceptions (when adding $P+P$, $P+\infty$, etc.). Furthermore for efficiency montgomery ladder is good for variable base but in signature you might use fixed based and in verification double base, and both favors Edwards. – Ruggero Jan 16 '17 at 10:41